Climate and the productivity, health, and peacefulness of society · 2018. 10. 10. · 1 Abstract...

Climate and the productivity, health, and peacefulness of society

by

Marshall Burke

A dissertation submitted in partial satisfaction of the

requirements for the degree of

Doctor of Philosophy

in

Agricultural and Resource Economics

in the

Graduate Division

of the

University of California, Berkeley

Committee in charge:

Associate Professor Maximilian Auffhammer, ChairProfessor Edward MiguelProfessor Alain de Janvry

Associate Professor Jeremy Magruder

Spring 2014


Copyright 2014by

Marshall Burke

1

Abstract


by

Marshall Burke

Doctor of Philosophy in Agricultural and Resource Economics

University of California, Berkeley

Associate Professor Maximilian Auffhammer, Chair

Mounting evidence that the global climate is changing has motivated a growingbody of work seeking to understand the likely impacts of these changes on economicoutcomes of interest. This dissertation studies the effects of variation in climateon three different outcomes: agricultural productivity in the United States, HIV inAfrica, and human conflict around the world. Along with the co-authors on thesepapers, I find that both short- and long-run increases in temperature are harmful toagricultural productivity in the US, that increased exposure to drought increases HIVprevalence in rural parts of Africa, and that increases in temperature and extremerainfall are associated with substantial increases in a variety of types of human con-flict. These findings have implications both for our understanding of the economicsof disease and conflict, and for how much societies might be willing to invest inemissions mitigation and adaptation in the face of future climate change.

i

To my daughters, who will inherit the climate we leave them.

ii

Contents

Contents ii

List of Figures iv

List of Tables vi

1 Overview 1

2 Adaptation to climate in US agriculture 32.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 32.2 Model and Empirical Approach . . . . . . . . . . . . . . . . . . . . . 82.3 Empirical Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 192.4 Alternate Explanations . . . . . . . . . . . . . . . . . . . . . . . . . . 282.5 Projections of impacts under future climate change . . . . . . . . . . 392.6 Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 40

3 Climate, economic shocks, and HIV in Africa 433.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 433.2 Conceptual Framework . . . . . . . . . . . . . . . . . . . . . . . . . . 463.3 Empirical Methods . . . . . . . . . . . . . . . . . . . . . . . . . . . . 483.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 563.5 Exploring Pathways . . . . . . . . . . . . . . . . . . . . . . . . . . . . 653.6 Macro level implications . . . . . . . . . . . . . . . . . . . . . . . . . 763.7 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 79

4 Climate and conflict 814.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 814.2 Estimation of climate-conflict linkages . . . . . . . . . . . . . . . . . . 844.3 Results from the quantitative literature . . . . . . . . . . . . . . . . . 904.4 Synthesis of findings . . . . . . . . . . . . . . . . . . . . . . . . . . . 94

iii

4.5 Implications for future climatic changes . . . . . . . . . . . . . . . . . 1024.6 Future research . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1034.7 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 107

Bibliography 112

A Adaptation to climate appendix 133A.1 Understanding changes in climate and agriculture over time . . . . . 133A.2 Correlates of trends in extreme heat . . . . . . . . . . . . . . . . . . . 137A.3 Robustness to outliers . . . . . . . . . . . . . . . . . . . . . . . . . . 138A.4 Choice of time period . . . . . . . . . . . . . . . . . . . . . . . . . . . 139A.5 Measurement error . . . . . . . . . . . . . . . . . . . . . . . . . . . . 146A.6 Effects on soy productivity . . . . . . . . . . . . . . . . . . . . . . . . 149A.7 Revenues and profits . . . . . . . . . . . . . . . . . . . . . . . . . . . 150A.8 Exit from agriculture . . . . . . . . . . . . . . . . . . . . . . . . . . . 153A.9 Additional evidence on selection . . . . . . . . . . . . . . . . . . . . . 154A.10 Why no adaptation . . . . . . . . . . . . . . . . . . . . . . . . . . . . 155A.11 Climate change projections . . . . . . . . . . . . . . . . . . . . . . . . 155

B Economic shocks and HIV appendix 159B.1 DHS Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 159B.2 Weather data and impact of drought on crop yields . . . . . . . . . . 160B.3 Shock Definition . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 161B.4 Estimating sample selection due to out-migration . . . . . . . . . . . 161B.5 Considering shock timing . . . . . . . . . . . . . . . . . . . . . . . . . 162B.6 The role of ARV Access . . . . . . . . . . . . . . . . . . . . . . . . . 164B.7 Estimating Changes in Sexual Behavior . . . . . . . . . . . . . . . . 164B.8 Country-level prevalence . . . . . . . . . . . . . . . . . . . . . . . . . 165

C Climate and conflict appendix 179C.1 Study selection, reanalysis and evaluation . . . . . . . . . . . . . . . . 179C.2 Evaluating and combining effect sizes . . . . . . . . . . . . . . . . . 190C.3 Publication bias . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 198C.4 Projected changes in temperature . . . . . . . . . . . . . . . . . . . . 201

iv

List of Figures

2.1 Change in temperature (oC), precipitation (%), and log cornyields over the period 1980-2000 for counties east of the 100thmeridian. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 5

2.2 Productivity of two different corn varieties as a function of tem-perature. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 10

2.3 Relationship between temperature and corn yields. . . . . . . . . 212.4 Estimates using various starting years and differencing lengths. 242.5 Percentage of the short run impacts of extreme heat on corn

productivity that are mitigated in the longer run. . . . . . . . . . 272.6 Projected impacts of climate change on corn yields by 2050. . . 41

3.1 Effect of rainfall shocks on African maize yields (left panel) andper capita GDP growth (right panel) . . . . . . . . . . . . . . . . 54

3.2 Effect of rainfall shocks on HIV, by severity (left panel) andtiming (right panel) . . . . . . . . . . . . . . . . . . . . . . . . . . . 65

3.3 Country-level HIV prevalence & Shocks . . . . . . . . . . . . . . . 78

4.1 Spatial and temporal coverage of the studies we review. . . . . . 834.2 Examples from studies of modern data. . . . . . . . . . . . . . . . 924.3 Examples of paleoclimate reconstructions that find associations

between climatic changes and human conflict . . . . . . . . . . . . 954.4 Modern estimates for the effect of climatic events on the risk of

interpersonal violence. . . . . . . . . . . . . . . . . . . . . . . . . . . 994.5 Modern estimates for the effect of climatic events on the risk of

intergroup conflict. . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1004.6 Projected temperature change by 2050 as a multiple of the local

historical standard deviation (σ) of temperature. . . . . . . . . . . 104

v

A.1 Changes in GDD and corn yield for corn-growing counties eastof the 100th meridian . . . . . . . . . . . . . . . . . . . . . . . . . . . 134

A.2 Map of changes in GDD 0-29C and GDD above 29C between1980-2000. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 135

A.3 Distributions of GDD > 29 for the 1980-2000 period (red lines)and as projected for 2050 across 18 climate models for the A1Bscenario (blue lines). . . . . . . . . . . . . . . . . . . . . . . . . . . . 136

A.4 Distribution of estimated annual growth in GDD > 29 for coun-ties in 13 corn belt states. . . . . . . . . . . . . . . . . . . . . . . . . 138

A.5 Observed versus simulated changes in GDD>29 . . . . . . . . . . 140A.6 Long difference estimates under various starting years and dif-

ferencing lengths. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 146A.7 Distribution of the change in average growing season tempera-

ture across our sample counties, for the period 1960-1980 (dot-ted line) or the period 1980-2000 (solid line). . . . . . . . . . . . . 147

A.8 Panel estimates of the effect of extreme heat on log corn yieldsby decade. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 148

A.9 Relationship between corn yields and temperature. . . . . . . . . 150A.10 Effects of extreme heat on soy yields under various starting years

and differencing lengths. . . . . . . . . . . . . . . . . . . . . . . . . . 151A.11 Projected changes in growing season temperature and precipi-

tation across US corn growing area by 2050. . . . . . . . . . . . . 158

B.1 Countries included in the study. Darker shades correspondingto higher HIV prevalence. . . . . . . . . . . . . . . . . . . . . . . . . 166

B.2 Pre-survey HIV trends, Low and High Prevalence Countries. . . 167B.3 Survival Following Seroconversion (East African population with-

out ARV) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 175B.4 Epidemic Curve . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 176B.5 People currently living with HIV, by year of seroconversion . . 177B.6 ARV Coverage Rates (2004-2009) . . . . . . . . . . . . . . . . . . . 178

C.1 Standardized effect sizes in Buhaug (2010b,a) and Burke et al.(2009a, 2010c). . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 182

C.2 Standardized effect sizes in Theisen (2012). . . . . . . . . . . . . . 188C.3 Conditional posterior means of the study-specific treatment ef-

fects. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 195C.4 Relationship between log of t-stat and log of the square root of

the degrees-of-freedom . . . . . . . . . . . . . . . . . . . . . . . . . . 199

vi

List of Tables

2.1 Comparison of long differences and panel estimates of the impacts oftemperature and precipitation on US corn yields . . . . . . . . . . . . . . 22

2.2 The effect of climate on yields estimated with a panel of differences. . . . 262.3 Effects of climate variation on crop revenues . . . . . . . . . . . . . . . . 322.4 Effects of climate variation on alternate adjustment margins . . . . . . . 342.5 Heterogenous effects of climate variation on corn yields . . . . . . . . . . 38

3.1 DHS Survey Information . . . . . . . . . . . . . . . . . . . . . . . . . . . 503.2 Shock Prevalence by Country . . . . . . . . . . . . . . . . . . . . . . . . 533.3 Effect of Shocks on HIV . . . . . . . . . . . . . . . . . . . . . . . . . . . 583.4 Robustness Checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 593.5 Robustness to sample selection from permanent migration . . . . . . . . 633.6 Placebo Tests . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 643.7 Exploring Behaviors: Increasing risky sexual behavior . . . . . . . . . . 733.8 Exploring Behaviors: Temporary migration . . . . . . . . . . . . . . . . . 743.9 Exploring Behaviors: Early school drop-out and marriage . . . . . . . . . 753.10 Exploring Behaviors: Impact on HIV by exposure to drought-induced

income shock . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 77

4.1 Unique quantitative studies testing for a relationship between climate andconflict, violence or political instability . . . . . . . . . . . . . . . . . . . 109

4.1 (continued) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1104.1 (continued) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 111

A.1 Yield response to GDD>29 across different panel and long difference mod-els, and variation in GDD>29 after accounting for fixed effects and otherclimate controls in these models. . . . . . . . . . . . . . . . . . . . . . . 139

A.2 Coefficients and p-values of univariate regressions of county characteristicson change in extreme heat exposure . . . . . . . . . . . . . . . . . . . . . 141

vii

A.3 Robustness of long difference results to addition of county control variables142A.4 Robustness of corn yield results to dropping outliers . . . . . . . . . . . . 143A.5 Robustness of results on alternate adaptations to removal of outliers . . . 144A.6 Long differences regressions with endpoints averaged over longer periods. 145A.7 Understanding measurement error through the comparison of panel esti-

mators . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 149A.8 Effects of Climate Variation on Input Expenditures . . . . . . . . . . . . 153A.9 Estimated Differences in Log Number of Farms by Amount of Warming . 155A.10 Effects of climate variation on equipment ownership. . . . . . . . . . . . 156A.11 Insurance take-up in 1998-2002 as a function of changes in GDD and

precipitation over 1980-2000. . . . . . . . . . . . . . . . . . . . . . . . . . 157

B.1 DHS Sampling for Serostatus Testing . . . . . . . . . . . . . . . . . . . . 168B.2 Non-response for Serostatus Testing . . . . . . . . . . . . . . . . . . . . . 169B.3 Non-response is not correlated with Shocks . . . . . . . . . . . . . . . . . 170B.4 Rainfall Shocks and Overall Variability . . . . . . . . . . . . . . . . . . . 171B.5 Impact of precipitation shocks on maize yields and per capita GDP growth. 172B.6 Vary Shock Definition: 10 to 20% . . . . . . . . . . . . . . . . . . . . . . 173B.7 Potential Loss in Rural Populations due to Shock-induced Migration . . 174B.8 ARV Awareness and Shocks . . . . . . . . . . . . . . . . . . . . . . . . . 176B.9 Shocks predict country-level HIV prevalence . . . . . . . . . . . . . . . . 178

C.1 Summary statistics for the distribution of effects across studies . . . . . . 193C.2 Posterior quantiles of treatment effects for the 10 studies on interpersonal

violence. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 196C.3 Posterior quantiles of treatment effects for the 21 studies on intergroup

conflict. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 197C.4 The relationship between log t-stat and log square root of the degrees-of-

freedom, using author-reported t-statistics. . . . . . . . . . . . . . . . . . 200

viii

Acknowledgments

I want to thank my advisors, Max Auffhammer and Ted Miguel, for their continualadvice, patience, and support. I would also like to thank all my co-authors on thiswork, Kyle Emerick, Erick Gong, Sol Hsiang, Kelly Jones, and Edward Miguel, fromwhom I learned (and continue to learn) an immense amount. I also thank the othermembers of my dissertation committee, Alain de Janvry and Jeremy Magruder, fortheir advice and encouragement.

I have also benefitted greatly from countless conversations and discussions at UCBerkeley and elsewhere, including with Betty Sadoulet, Sam Heft-Neal, ChristianTraeger, Ethan Ligon, Lauren Falcao, Roz Naylor, Walter Falcon, Jen Burney, andperhaps most importantly David Lobell.

Finally, thanks to my family and friends, who along with my colleagues havemade the last five years immensely enjoyable. Thanks to my parents for sowing theseeds, purposefully or inadvertently, of an academic career. And the biggest thanksto my beautiful wife and daughters, who are thankfully bad for productivity in theshort-run but probably good for it over the long-run.

1

Chapter 1

Overview

This dissertation combines research on three topics in applied empirical economics.Each of the papers tries to shed light on how changes in environmental conditions– climate in particular – shape a particular economic outcome of interest. Thepapers have implications for our understanding of the broader determinants of theseoutcomes, as well as implications for important policy decisions around climate.

In the first paper, which is joint work with Kyle Emerick, we study how agentsmight adapt to a changing climate. In particular, we exploit large variation in recenttemperature and precipitation trends to identify adaptation to climate change inUS agriculture, and use this information to generate new estimates of the potentialimpact of future climate change on agricultural outcomes. We show that longer-runadaptations appear to have mitigated less than half – and more likely none – of thelarge negative short-run impacts of extreme heat on productivity. We then show thatthis limited recent adaptation implies substantial losses under future climate changein the absence of countervailing investments.

In the second paper, which is joint work with Erick Gong and Kelly Jones, weexamine how variation in local economic conditions – as proxied by changes in localprecipitation – has shaped the HIV/AIDS epidemic in Africa. Using data from over200,000 individuals across 19 countries, we match biomarker data on individuals’HIV status to information on local rainfall shocks, a large source of variation in in-come for rural households. We estimate that infection rates in HIV-endemic ruralareas increase by 11% for every recent drought, an effect that is statistically andeconomically significant. Income shocks explain up to 20% of the variation in HIVprevalence across African countries, suggesting that existing approaches to HIV pre-vention could be bolstered by efforts to help poor households better manage incomerisk.

The third paper, which is joint work with Solomon Hsiang and Edward Miguel,

CHAPTER 1. OVERVIEW 2

examines whether human conflict can be affected by climatic changes. Drawingfrom archaeology, criminology, economics, geography, history, political science, andpsychology, we assemble and analyze the 60 most rigorous quantitative studies anddocument a substantial convergence of results. We find strong causal evidence link-ing climatic events to human conflict across a range of spatial and temporal scalesand across all major regions of the world. The magnitude of climate’s influence issubstantial: for each 1 standard deviation (1σ) change in climate towards warmertemperatures or more extreme rainfall, median estimates indicate that the frequencyof interpersonal violence rises 4% and the frequency of intergroup conflict rises 14%.Because locations throughout the inhabited world are expected to warm 2-4σ by2050, amplified rates of human conflict could represent a large and critical impact ofanthropogenic climate change.

3

Chapter 2

Adaptation to climate in USagriculture

2.1 Introduction*

How quickly economic agents adjust to changes in their environment is a centralquestion in economics, and is consequential for policy design across many domains(Samuelson, 1947; Viner, 1958; Davis and Weinstein, 2002; Cutler, Miller, and Nor-ton, 2007; Hornbeck, 2012a). The question has been a theoretical focus since atleast Samuelson (1947), but has gained particular recent salience in the study of theeconomics of global climate change. Mounting evidence that the global climate ischanging (Meehl et al., 2007a) has motivated a growing body of work seeking tounderstand the likely impacts of these changes on economic outcomes of interest.Because many of the key climatic changes will evolve on a time-scale of decades, thekey empirical challenge is in anticipating how economic agents will adjust in lightof these longer-run changes. If adjustment is large and rapid, and such adjustmentlimits the resulting economic damages associated with climate change, then the rolefor public policy in addressing climate change would appear limited. But if agentsappear slow or unable to adjust on their own, and economic damages under climatechange appear likely to otherwise be large, then this would suggest a much moresubstantial role for public policy in addressing future climate threats.

To understand how agents might adapt to a changing climate, an ideal but impos-sible experiment would observe two identical Earths, gradually change the climateon one, and observe whether outcomes diverged between the two. Empirical ap-

*The material from this chapter is a co-authored working paper with Kyle Emerick titled:“Adaptation to climate change: Evidence from US agriculture”.

CHAPTER 2. ADAPTATION TO CLIMATE IN US AGRICULTURE 4

proximations of this experiment have typically either used cross-sectional variationto compare outcomes in hot versus cold areas (e.g. Mendelsohn, Nordhaus, andShaw (1994); Schlenker, Hanemann, and Fisher (2005)), or have used variation overtime to compare a given area’s outcomes under hotter versus cooler conditions (e.g.Deschenes and Greenstone (2007); Schlenker and Roberts (2009a); Deschenes andGreenstone (2011); Dell, Jones, and Olken (2012a)). Due to omitted variables con-cerns in the cross-sectional approach, the recent literature has preferred the latterpanel approach, noting that while average climate could be correlated with othertime-invariant factors unobserved to the econometrician, short-run variation in cli-mate within a given area (typically termed “weather”) is plausibly random and thusbetter identifies the effect of changes in climate variables on economic outcomes.

While using variation in weather helps to solve identification problems, it perhapsmore poorly approximates the ideal climate change experiment. In particular, ifagents can adjust in the long run in ways that are unavailable to them in the shortrun1, then impact estimates derived from shorter-run responses to weather mightoverstate damages from longer-run changes in climate. Alternatively, there could beshort-run responses to inclement weather, such as pumping groundwater for irrigationin a drought year, that are not tenable in the long-run if the underlying resource isdepletable (Fisher et al., 2012). Thus it is difficult to even sign the “bias” implicitin estimates of impacts derived from short-run responses to weather.

In this paper we exploit variation in longer-term changes in temperature andprecipitation across the US to identify the effect of climate change on agriculturalproductivity, and to quantify whether longer-run adjustment to changes in climatehas indeed exceeded shorter-run adjustment. Recent changes in climate have beenlarge and vary substantially over space: as shown in Figure 2.1, temperatures insome counties fell by 0.5◦C between 1980-2000 while rising 1.5◦C in other counties,and precipitation across counties has fallen or risen by as much as 40% over the sameperiod. We adopt a “long differences” approach and model county-level changes inagricultural outcomes over time as a function of these changes in temperature andprecipitation, accounting for time-invariant unobservables at the county level andtime-trending unobservables at the state level.

This approach offers three distinct advantages over existing work. First, un-like either the panel or cross-sectional approaches, it closely replicates the idealizedclimate change impact experiment, quantifying how farmer behavior responds tolonger-run changes in climate while avoiding concerns about omitted variables bias.Second, observed variation in these recent climate changes largely spans the range

1e.g. Samuelson’s famed Le Chatelier principle, in which demand and supply elasticities arehypothesized to be smaller in the short run than in the long run due to fixed cost constraints.


Figure 2.1: Change in temperature (oC), precipitation (%), and log cornyields over the period 1980-2000 for counties east of the 100th meridian.

Temperature

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change in yield (log)

−0.5 0.0 0.5 1.0

Temperature and precipitation are measured over the main April - September growing sea-son. Colors for each map correspond to the colored bins in the histogram beneath the plot.

of projected near-term changes in temperature and precipitation provided by globalclimate models, allowing us to make projections of future climate change impactsthat do not rely on large out-of-sample extrapolations. Finally, by comparing howoutcomes respond to longer-run changes in climate to how they respond to shorterrun fluctuations as estimated in the typical panel model, we can test whether theshorter-run damages of climatic variation on agricultural outcomes are in fact mit-igated in the longer-run. Quantifying this extent of recent climate adaptation inagriculture is of both academic and policy interest, and a topic about which thereexists little direct evidence.

We find that productivity of the primary US field crops, corn and soy, is sub-stantially affected by these long-run trends in climate. Our main estimate for cornsuggests that spending a single day at 30◦C (86◦F) instead of the optimal 29◦C re-duces yields at the end of the season by about half a percent, which is a large effect.2

2The within-county standard deviation of days of exposure to “extreme” temperatures above29◦C is 30, meaning a 1SD increase in exposure would reduce yields by 15%.


The magnitude of this effect is net of any adaptations made by farmers over the 20year estimation period, and is robust to using different time periods and differencinglengths.

To quantify the magnitude of any yield-stabilizing adaptations that have oc-curred, we then compare these long differences estimates to panel estimates of short-run responses to weather. Long run adaptations appear to have mitigated less thanabout half of the short-run effects of extreme heat exposure on corn yields, and pointestimates across a range of specifications suggest that long run adaptions have morelikely offset none of these short run impacts. We also show limited evidence foradaptation along other margins within agriculture: revenues are similarly harmedby extreme heat exposure, and farmers do not appear to be substantially alteringthe inputs they use nor the crops they grow in response to a changing climate.

We then examine different explanations for why adjustment to recent climatechange has been minimal. For instance, adaptation could be limited because thereare few adjustment opportunities to exploit, or alternatively because farmers don’trecognize that climate has in fact changed and that adaptation is needed. Which it isis important for how we interpret our results, and in particular how they extrapolateto future warming scenarios. If farmers failed to adapt in the past because they didnot recognize the climate was changing, but in the future they become aware of thesechanges and quickly adapt, then our findings would be a poor guide to future impactsof warming. On the other hand, if farmers had recognized the need for adaptationbut were unable to do so, then their past responses to extreme heat exposure wouldprovide a plausible “business-as-usual” benchmark for the impacts of future warmingin the absence of novel investment in adaptation.

While we cannot directly observe farmer perceptions of climate change, there isboth theoretical and empirical guidance on which locations should be more likelyto have learned about the negative effects of extreme heat or to have recognizedthat the climate was changing: locations that faced larger exposure to extreme heatin an earlier period, locations where the underlying temperature variance is lower(making any warming “signal” stronger), locations with better educated farmers,or locations where voting behavior suggest that a belief in climate change is morelikely. We find no evidence that farmers in such areas responded any differently toextreme heat exposure than farmers previously un-exposed, less educated, or in moreclimate-change-skeptical regions, providing some evidence that adaptation was notlimited by a failure of recognition.

As a final exercise, we combine our long differences estimates with output from18 global climate models to project the impacts of future climate change on theproductivity of corn, a crop increasingly intertwined with the global food and fueleconomy. Such projections are an important input to climate policy discussions, but


bear the obvious caveat that future adjustment capabilities are constrained to whatfarmers were capable of in the recent past. Nevertheless, because our projectionsare less dependent on large out-of-sample extrapolation, and because they accountfor farmers’ recent ability to adapt to longer-run changes in climate, we believe theyare a substantial improvement over existing approaches. Our median estimate isthat corn yields will be about 15% lower by mid-century relative to a world withoutclimate change, with some climate models projecting losses as low as 7% and othersas high as 64%. Valued at current prices and production quantities, this fall incorn productivity in our sample counties would generate annual losses of $6.7 billiondollars by 2050. We note that a 15% yield loss is on par with expected yield lossesresulting from the well-publicized “extreme” drought and heat wave that struck theUS midwest in the summer of 2012. Given the substantial role that corn plays inUS agricultural production and the dominant role that the US plays in the globaltrade of corn, these results imply substantial global damages if the more negativeoutcomes in this range are realized.

Our work contributes to the rapidly growing literature on climate impacts, and inparticular to a host of recent work examining the potential impacts of climate changeon US agriculture (Mendelsohn, Nordhaus, and Shaw, 1994; Schlenker, Hanemann,and Fisher, 2005; Deschenes and Greenstone, 2007; Schlenker and Roberts, 2009a;Fisher et al., 2012). We build on this work by directly quantifying how farmers haveresponded to longer-run changes in climate, and are able to construct projections offuture climate impacts that account for this observed ability to adjust.

Methodologically our work is closest to Dell, Jones, and Olken (2012a) and toLobell and Asner (2003). Dell, Jones, and Olken (2012a) focus on panel estimatesof the impacts of country-level temperature variation on economic growth, but alsouse cross-country differences in recent warming to estimate whether there has been“medium-run” adaptation. Their point estimates suggest little difference betweenresponses to short-run fluctuations and medium-run warming, but estimates for thelatter are imprecise and not always significantly different from zero, meaning thatlarge adaptation cannot be ruled out. Lobell and Asner (2003) study the effectof trends in average temperature on trends in US crop yields, finding that warmeraverage temperatures are correlated with declining yields. We build on this work byproviding more precise estimates of recent adaptation, and by accounting more fullyfor time-trending unobservables that might otherwise bias estimates.

Our findings also relate to a broader literature on long-run economic adjustments.A body of historical research suggests that economic productivity often substantiallyrecovers in the longer run after an initial negative shock (Davis and Weinstein, 2002;Miguel and Roland, 2011), and that in the long run farmers in particular are ableto exploit conditions that originally appeared hostile (Olmstead and Rhode, 2011).


Somewhat in contrast, Hornbeck (2012a) exploits variation in soil erosion duringthe 1930’s American Dust Bowl to show that negative environmental shocks canhave substantial and lasting effects on productivity. Using data from a more recentperiod, we examine responsiveness to a slower-moving environmental “shock” thatis very representative of what future climate change will likely bring. Similar toHornbeck, we find limited evidence that agricultural productivity has adapted tothese environmental changes, with fairly negative implications for the future impactsof climate change on the agricultural sector.

The remainder of this paper is organized as follows. In Section 2 we develop asimple model of farmer adaptation and use it to motivate our estimation approach.Section 3 describes our main results on the extent of past adaptation. In Section4 we try to rule out alternative explanations for our results. Section 5 uses datafrom global climate models to build projections of future yield impacts, and Section6 concludes and discusses implications for policy.

2.2 Model and Empirical Approach

Agriculture is a key sector where future climate change is estimated to have largedetrimental effects, and is a primary focus of the empirical literature on climatechange impacts. To formalize the ways in which our identification of climate im-pacts differs from that of the past literature, we develop a simple model of farmeradaptation, building on earlier work by Kelly, Kolstad, and Mitchell (2005). Theclimate literature generally understands adaptation as any adjustment to a changingenvironment that exploits beneficial opportunities or moderates negative impacts.3

Adaptation thus requires an agent to recognize that something in her environmenthas changed, to believe that an alternative course of action is now preferable to hercurrent course, and to have the capability to implement that alternative course.

We consider a farmer facing a choice about which of two crop varieties to grow,where one performs relatively better in cooler climates (variety 1) and the otherin warmer climates (variety 2). We assume this relative performance is known tothe farmer. Denote the choice of variety for farmer i as xit ∈ {0, 1}, with xit = 1the choice to grow the relatively heat-tolerant variety 2. The output of farmer i inperiod t is yit = f(xit, zit), where zit is realized temperature in period t and is drawnfrom a normal distribution ∼ N(ωt, σ

2). We assume a quadratic overall productiontechnology with respect to temperature:

yit = β0 + β1zit + β2z2it + xit(α0 + α1zit + α2z

2it) (2.1)

3See Zilberman, Zhao, and Heiman (2012) and Burke and Lobell (2010) for an overview.


with production for the conventional variety given by β0 + β1zit + β2z2it, and the

differential productivity between the conventional and heat-tolerant varieties givenby α0 + α1zit + α2z

2it.

The farmer in year i chooses xit to maximize expected output prior to realizingweather. The heat-tolerant crop will be chosen if E(α0 + α1zit + α2z

2it) > 0, which

can be rewritten asα0 + α1ωt + α2(ω2

t + σ2) > 0. (2.2)

We assume that the α and β parameters are known to the farmer but not to theeconometrician. Figure 2.2 displays the productivity of the two varieties as a functionof temperature. As drawn, the productivity frontiers have similar concavity4 (α2 ≈ 0)such that the perfectly informed farmer adopts the heat-tolerant crop when theexpected temperature exceeds ω.

We incorporate climate change as a shift in mean temperature from ω → ω′,with ω < ω < ω′. In keeping with evidence from climate science (see Meehl et al.(2007a)), we assume that this increase in mean is not accompanied by a change invariance, such that after climate change the farmer experiences zit ∼ N(ω′, σ2) ineach year. A fully informed farmer recognizes this change and immediately adoptsthe heat-tolerant crop, which we consider “adaptation”. In reality, farmers likelylearn about changes in climate over time and only adjust behavior after acquiringstrong enough information that climate has changed. Following Kelly, Kolstad, andMitchell (2005), we assume this learning follows a simple Bayesian process where thefarmer has an prior belief about ωt but knows that this belief is imperfect. We denotethe belief as µt and its variance as 1/τt, such that in period t the farmer believesω ∼ N(µt, 1/τt). In each period she observes zit and updates her belief about theaverage temperature to µt+1 using a weighted combination of her prior belief and thenew climate realization she experiences. Letting ρ = 1/σ2, the farmer’s belief aboutmean climate after T years is given by (DeGroot, 1970):

µT =τtµt + Tρzitτt + Tρ

(2.3)

4A negative value of α2 would indicate that productivity of the heat-tolerant crop is moreresponse to temperature changes (i.e. the productivity or profit frontier for the heat-tolerant crop is“more concave”). In this case, if climate variability is large, then the expected gain from adaptationat average climate must be large enough to offset expected losses in bad years. With α2 > 0, theresponse function for the heat tolerant crop is “flatter” such that the farmer is willing to adopt theheat tolerant crop before the intersection of the two curves because of the increased certainty thatit provides.


Figure 2.2: Productivity of two different corn varieties as a function oftemperature.

yield, pro�t

(a)

(b)

temperature

(c)

ω’ω ω

v0

v1

v2

Variety 1

Variety 2

Equilibriumimpact

Adaptation

With τt+1 = τt + ρ, then in expectation it follows that:

µT − ω′ =τ0(µ0 − ω′)τ0 + Tρ

(2.4)

Equation (2.4) has two important implications: beliefs about mean temperatureconverge to the true value as the number of time periods increases (T ↑), and convergemore quickly when there is less variance in annual temperature (i.e. when ρ is larger).This suggests that farmers should be more likely to recognize changes in climate –and thus adapt to those changes, if information is a constraint to adaptation – inareas where the temperature variance is low, and when they are given more time toobserve realizations of the new climate. We use these predictions to help us interpretour main findings in what follows.


Existing approaches

Returning to Figure 2.2, the long-term damages imposed by a shift in climate willbe v0 − v1 if adaptation takes place.5 Past literature has taken two approachesto estimating this quantity. In pioneering work, Mendelsohn, Nordhaus, and Shaw(1994) use cross-sectional variation in average temperature and precipitation (andtheir squares) to explain variation in agricultural outcomes across US counties. Thecross sectional specification is

yi = α + β1wi + β2w2i + ci + εi, (2.5)

where yi is some outcome of interest in county i, wi is again the average temperature,and ci other time invariant factors affecting outcomes (such as soil quality). Mendel-sohn et al’s preferred dependent variable is land values, which represent the presentdiscounted value of the future stream of profits that could be generated with a givenparcel of land, and thus in principle embody any possible long-run adaptation to av-erage climate. Therefore, a county with average temperature of ω will achieve v0 onaverage, a county with average temperature of ω′ will achieve v1, and the estimatesof β1 and β2 along with a projected rise in average temperatures from ω to ω′ wouldseem to identify the desired quantity of v0 − v1.

Cross sectional models in this setting make an oft-criticized assumption: thataverage climate is not correlated with other unobserved factors (the ci – soil quality,labor productivity, technology availability etc) that also affect outcomes of interest(Schlenker, Hanemann, and Fisher, 2005; Deschenes and Greenstone, 2007). Giventhese omitted variables concerns, more recent work has used panel data to explorethe relationship between agricultural outcomes and variation in temperature and pre-cipitation (Deschenes and Greenstone (2007); Schlenker and Roberts (2009a); Welchet al. (2010); Lobell, Schlenker, and Costa-Roberts (2011)).6 The data generatingprocess in this approach is:

yit = α + β1zit + β2z2it + ci + εit (2.6)

All time invariant factors are absorbed by the location fixed effects ci, and impactsof temperature and precipitation on (typically annual) outcomes are thus identified

5Kelly, Kolstad, and Mitchell (2005) call this the “equilibrium response”, in contrast to thecosts incurred when undertaking adaptation (e.g. the purchase of a more expensive heat-tolerantvariety), which they term “adjustment costs”.

6Examples in the climate literature outside of agriculture include Burke et al. (2009b); Deschenesand Greenstone (2011); Auffhammer and Aroonruengsawat (2011); Dell, Jones, and Olken (2012a).


from deviations from location-specific means.7 Because this year-to-year variation intemperature and precipitation (typically termed “weather”) is plausibly exogenous,fixed effects regressions overcome omitted variables concerns with cross-sectionalmodels, and the effect of temperature on outcomes such as yield or profits can beinterpreted causally.

Many studies then combine the estimated short-run responses from panel re-gressions with output from global climate models to project potential impacts underfuture climate change.8 In making these projections, the implicit assumption is againthat short-run responses to variation in weather are representative of how farmerswill respond to longer-run changes in average climate. It is not obvious this will bethe case. Consider a panel covering many years, with a temperature rise from ω to ω′

occuring somewhere within these years. The panel model would identify movementalong either one of the two curves shown in Figure 2.2, with the point estimate beinga weighted average of the slopes of the two curves, with weights depending on if andwhen the varietal switch occurred. If the heat-tolerant crop is adopted at the end ofthe period then fixed effects estimates will be heavily weighted towards the curve forthe conventional crop, overstating equilibrium losses. If adaptation is instantaneousthen fixed effects estimates trace out the curve for the heat-tolerant crop, whichcould understate impacts if (as drawn) the slope of the response function is positiveat ω′. Thus estimates of short-run responses to weather will not even bound esti-mates of longer-run response to climate. Panel models therefore solve identificationproblems in the cross-sectional approach, at the cost of more poorly approximatingthe idealized climate change experiment.

7McIntosh and Schlenker (2006) show that including a quadratic term in the standard panelfixed effects model allows unit means to re-enter the estimation. Inclusion of a squared termtherefore results in impacts of the independent variable of interest being derived not only fromwithin-unit variation over time but also from between-unit variation in means. In principle, thiswould allow for estimation of the outer as well as the inner envelope, a strategy explored bySchlenker (2006), although it is not clear that omitted variables concerns have not also re-enteredthe estimation along with the unit means. In any case, growing degree days allow temperatureto enter non-linearly without the complication of the quadratic term, and we exploit this factto generate estimates of adaptation. Furthermore, using trends in climate to identify climatesensitivities remains an arguably more “direct” approach to understanding near-term impacts offuture climate change, and is thus the approach we take here.

8See Burke et al. (2013) for a review of these studies and for the use of global climate modelsin this context.


The long differences approach

We attempt to simultaneously overcome the limitations of both the cross-sectionaland panel approaches by long differencing. We use (2.6) to construct longer run yieldand temperature averages at two different points in time for a given location, andcalculate changes in average yields as a function of changes in average temperature.Consider two multi-year periods denoted “a” and “b”, each spanning n years. Ourapproach is to separately sum (2.6) over all the years in each period, e.g. with theaverage yield in period a given by yia = 1

n

∑t∈a yit and average temperature zia

representing the averaged zit’s over the same period. Equation (2.6) for period abecomes:

yia = α + β1zia + β2zia2 + ci + εia. (2.7)

Defining period b similarly, we can “long difference” over the two periods to get:

yib − yia = β1(zib − zia) + β2(zib2 − zia2) + (ci − ci) + (εib − εia) (2.8)

The time-invariant factors drop out, and we can rewrite as:

∆yi = β1∆zi + β2∆(zi)2 + ∆εi, (2.9)

Generating unbiased estimates of β1 and β2 requires that changes in temperaturebetween the two periods are not correlated with time-varying unobservables thatalso affect outcomes of interest. Below we provide evidence that differential climatetrends across our sample of US counties are likely exogenous and surprisingly large.

Estimating the impact of climate on agricultural productivity with the long dif-ferences approach in (2.9) offers substantial advantages over both the cross-sectionaland panel approaches. First, it arguably better approximates the ideal “parallelworlds” experiment. That experiment randomly assigns climate trends to differentearths, and the long differences approximation utilizes variation in longer-run cli-mate change that are unlikely to be correlated with variables that explain changes inyield. Second, unlike the cross-sectional approach, the long differences estimates areimmune to time-invariant omitted variables, and unlike the panel approach the rela-tionship between climate and agricultural productivity is estimated from long-termchanges in average conditions instead of short-run year-to-year variation. Finally,because long differences estimates will embody any adaptations that farmers haveundertaken to recent trends, and because the range in these trends falls within therange of projected climate change over at least the next three decades, then projec-tions of future climate change impacts on agricultural productivity based on longdifferences estimates would appear more trustworthy than those based on eitherpanel or cross-sectional methods.


We then use this strategy to quantify the extent of recent adaptation in USagriculture, comparing our long differences estimates to those from an annual panelmodel. We would interpret more positive long difference estimates as evidence ofadaptation: that farmers are better able to adjust to longer-run changes in climatethan they are to shorter-run changes in weather. In Figure 2.2, if any adaptationtakes place, the long differences approach should identify v0 − v1. If no adaptationoccurs, then long difference regressions will identify v0 − v2, i.e. the same damagesidentified by fixed effects. We attempt to rule out other explanations for divergencebetween panel and long-differences estimates - e.g. measurement error, or adaptationoutside of agriculture - in Section 2.4.

Data and estimation

Our agricultural data come from the United States Department of Agriculture’sNational Agricultural Statistics Service. Crop area and yield data are available at thecounty-year level, and economic measures of productivity such as total revenues andagricultural land values are available every five years when the Agricultural Censusis conducted.9 Our unit of observation is thus the county, and in keeping with theliterature we focus the main part of the analysis on counties that are east of the 100thmeridian. The reason for this is that cropland in the American West typically relieson highly subsidized irrigation systems, and the degree of adaptation embodied inthe use and expansion of these systems might poorly extrapolate to future scenariosas the federal government is unlikely to subsidize new water projects as extensivelyas it has in the past (Schlenker, Hanemann, and Fisher, 2005). Over the last decade,the counties east of the 100th meridian accounted for 93% of US corn productionand 99% of US soy production.

Our climate data are from Schlenker and Roberts (2009a) and consist of dailyinterpolated values of precipitation totals and maximum and minimum temperaturesfor 4 km grid cells covering the entire United States over the period 1950-2005. Thesedata are aggregated to the county-day level by averaging daily values over the gridcells in each county where crops are grown, as estimated from satellite data.10

Past literature has demonstrated strong non-linearities in the relationship be-tween temperature and agricultural outcomes (e.g. Schlenker and Roberts (2009a)).Such non-linearities are generally captured using the concept of growing degree days(GDD). GDD measure the amount of time a crop is exposed to temperatures be-tween a given lower and upper bound, with daily exposures summed over the growing

9We thank Michael Roberts for sharing additional census data that are not yet archived online.10We thank Wolfram Schlenker for sharing the weather data and the code to process them.


season to get a measure of annual growing degree days. Denoting the lower boundas tl and the upper bound as th, if td is the average temperature on a given day d,then degree days for that day are calculated as:

GDDd;tl:th =

0 if td ≤ tl

td − tl if tl < td ≤ thth − tl if th < td

Daily degree days are then summed over all the days in the growing season (typicalApril 1 to September 30th for corn in the United States) to get an annual measureof GDD.

Using this notion of GDD, and using the county agricultural data described above,we model agricultural outcomes as a simple piecewise linear function of temperatureand precipitation.11 We estimate the long differences model:

∆yis = β1∆GDDis;l0:l1+β2∆GDDis;l1:∞+β3∆Precis;p<p0+β4∆Precis;p>p0+αs+∆εis,(2.10)

where ∆yis is the change in some outcome y in county i in state s between twoperiods. In our main specification these two periods are 1980 and 2000, and wecalculate endpoints as 5-year averages to more effectively capture the change inaverage climate or outcomes over time. That is, for the 1980-2000 period we takeaverages for each variable over 1978-1982 and over 1998-2002, and difference thesetwo averages.

The lower temperature “piece” in (2.10) is the sum of GDD between the boundsl0 and l1, and ∆GDDis;l0:l1 term gives the change in GDD between these boundsover the two periods. The upper temperature “piece” has a lower bound of l1 andis unbounded at the upper end, and the ∆GDDis;l1:∞ term measures the change inthese GDD between the two periods.12 We also measure precipitation in a countyas a piecewise linear function with a kink at p0. The variable Precis;p<p0 is thereforethe difference between precipitation and p0 interacted with an indicator variable

11We choose the piecewise linear approach for two reasons. First, existing work on US agriculturalresponse to climate suggests that a simple piecewise linear function delivers results very similar tothose estimated with much more complicated functional forms (Schlenker and Roberts, 2009a).Second, these other functional forms typically feature higher order terms, which in a panel settingmeans that unit-specific means re-enter the estimation (McIntosh and Schlenker, 2006). This notonly raises omitted variables concerns, but it complicates our strategy for estimating the extent ofpast adaptation by comparing long differences with panel estimates; in essence, identification in thepanel models in no longer limited to location-specific variation over time.

12As an example, if l0 = 0 and l0 = 30, then a given set of observed temperatures -1, 0, 1, 10,29, 31, and 35 would result in GDDis;l0:l1 equal to 0, 0, 1, 10, 29, 30, and 30, and GDDis;l1:∞ equalto 0, 0, 0, 0, 1, and 5.


for precipitation being below the threshold p0. Precis;p>p0 is similarly defined forprecipitation above the threshold.13 In the estimation we set l0 = 0 and allow thedata to determine l1 and p0 by looping over all possible thresholds and selecting themodel with the lowest sum of squared residuals.

Importantly, we also include in (2.10) a state fixed effect αs which controls forany unobserved state-level trends. This means that identification comes only fromwithin-state variation, eliminating any concerns of time-trending unobservables atthe state level. Finally, to quantify the extent of recent adaptation, we estimatea panel version of (2.10), where observations are at the county-year level and theregression includes county and year fixed effects. As suggested by earlier studies(e.g. Schlenker and Roberts (2009a)), the key coefficient in both models is likely tobe β2, which measures how corn yields are affected by exposure to extreme heat. Iffarmers adapt significantly to climate change then we would expect the coefficientβ2 to be significantly larger in absolute value when estimated with panel fixed effectsas compared to our long differences approach. The value 1 − βLD2 /βFE2 , gives thepercentage of the negative short-run impact that is offset in the longer run, and isour measure of adaptation to extreme heat.

Figure 1 displays the variation that is used in our identification strategy. Some UScounties have cooled slightly over the past 3 decades, while others have experiencedwarming equivalent to over 1.5 times the standard deviation of local temperature.Differential trends in precipitation over the 1980-2000 have been similarly large, withprecipitation decreasing by more than 30% in some counties and increasing by 30% inothers. By way of comparison, the upper end of the range in these recent temperaturetrends is roughly equivalent to the mean warming projected by global climate modelsto occur over US corn area by 2030, and the range in precipitation trends almostfully contains the range in climate model projections of future precipitation changeover the same area by the mid-21st century. More importantly, substantial varia-tion is apparent within states. For instance, Lee County in the southeastern Iowaexperienced an increase in average daily temperature during the main corn growingseason of 0.46◦C, and Mahaska county – approximately 80 miles to the northwest –experienced a decrease in temperature of 0.3◦C over the same period. Corn yields inparts of northern Kentucky declined slightly while rising by 20-30% only 100 milesto the south.

While we explore robustness of our results to different time periods and differ-encing lengths, we focus on the post-1980 period for a number of reasons. First,

13A simple example is useful to illustrate the differencing of precipitation variables when thethreshold is crossed between periods. Consider a county with an increase in average precipitationfrom 35 mm in 1980 to 50 mm in 2000. If the precipitation threshold is 40 mm, then ∆Precis;p<p0

=5 and ∆Precis;p>p0

= 10.


warming trends since 1980 were much larger than in earlier periods. For instance,over the 1960-1980 period, only half of the counties in our sample experienced av-erage warming, and none experience warming of more than 1C (see Figure A.7).Second, recognition of climate change was much higher in this later period, whichhelps alleviate some concerns that a lack of recognition of climate change is what isdriving our results. In particular, prior to 1980 there was even significant scientificand popular concern about the risks from “global cooling” (e.g. Gwynne (1975)),and only during the 1980’s and 1990’s was there growing recognition that the climatewas warming and that increasing greenhouse gas emissions meant there would verylikely be further warming in the future.

Section A.1 in the Appendix more rigorously quantifies the variation in temper-ature used in the long differences estimation. We document that observed tempera-ture changes over the period do in fact represent meaningful long-run changes ratherthan just short-run variation around endpoint years, and we show that the residualvariation in these temperature changes remains large (relative to projected futurechanges) after accounting for state fixed effects.

Are recent climate trends exogenous?

There are a few potential violations to the identifying assumption in (2.10). The firstis that trends in local emissions could affect both climate and agricultural outcomes.In particular, although greenhouse gases such as carbon dioxide typically become“well mixed” in the atmosphere soon after they are emitted, other species such asaerosols are taken out of the atmosphere by precipitation on a time scale of days,meaning that any effect they have will be local. Aerosols both decrease the amount ofincoming solar radiation, which cools surface temperatures and lowers soil evapora-tion, and they tend to increase cloud formation, although it is somewhat ambiguouswhether this leads to an increase in precipitation. For instance, Leibensperger et al.(2011) found that peak aerosol emissions in the US during the 1970s and 1980s re-duced surface temperatures over the central and Mid-Atlantic US by up to 1oC, andled to modest increases in precipitation over the same region.

The effect of aerosols on crops is less well understood (Auffhammer, Ramanathan,and Vincent, 2006). While any indirect effect through temperature or precipitationwill already be picked up in the data, aerosols become an omitted variables concernif their other influence on crops – namely their effect on solar radiation – have im-portant effects on crop productivity. Because crop productivity is generally thoughtto be increasing and concave in solar radiation, reductions in solar radiation arelikely to be harmful, particularly to C4 photosynthesis plants like corn that do not


become light saturated under typical conditions.14 However, aerosols also increasethe “diffuse” portion of light (think of the relatively even light on a cloudy day),which allows additional light to reach below the canopy, increasing productivity. Arecent modeling study finds negative net effects for corn, with aerosol concentrations(circa the year 2000) reducing corn yields over the US midwest by about 10%, albeitwith relatively large error bars. This would make it likely that, if anything, aerosolswill cause us to understate any negative effect of warming on crop yields: aerosolslead to both cooling (which is generally beneficial in our sample) and to a reductionin solar radiation (which on net appears harmful for corn). In any case, the inclusionof state fixed effects means that we would need significant within-state variation inaerosol emissions for this to be a concern.

The second main omitted variables concern is changes in local land use. Evi-dence from the physical sciences suggests that conversion between types of land (e.g.conversion of forest to pasture, or pasture to cropland), or changes in managementpractices within pre-existing farmland (e.g. expansion of irrigation) can have signif-icant effects on local climate. For instance, expansion in irrigation has been shownto cause local cooling (Lobell, Bala, and Duffy, 2006), which would increase yieldsboth directly (by reducing water stress) and indirectly (via cooling), leading to apotential omitted variables problem. The main empirical difficulty is that local landuse change could also be an adaptation to changing climate – i.e. a consequenceof a changing climate as well as a cause. In the case of irrigation, adaptation andirrigation-induced climate change are likely to go in opposite directions: if irrigationis an omitted variable problem, we would need to see greater irrigation expansion incooler areas, whereas if irrigation is an adaptation, we would expect relatively moreexpansion in warm areas. Overall, though, because we see little change in either landarea or land management practices, we believe these omitted variables concerns tobe limited as well.

The most recent evidence from the physical sciences suggests that the large dif-ferential warming trends observed over the US over the past few decades are likelydue to natural climate variability - in particular, to variation in ocean tempera-tures and their consequent effect on climate over land (e.g. Meehl, Arblaster, andBranstator (forthcoming)). As such, these trends appear to represent a true “natu-ral experiment”, and are likely exogenous with respect to the outcomes we wish tomeasure. Nevertheless, as a final check on exogeneity, we show in Table A.2 that the

14Crops that photosynthesize via the C3 pathway, which include wheat, rice, and soybeans,become ”light saturated” at one-third to one-half of natural sunlight, meaning that reductions insolar radiation above that threshold would have minimal effects on productivity. C4 plants such ascorn do not light saturate under normal sunlight, so are immediately harmed by reductions in solarradiation (Greenwald et al. (2006)).


within-state change in exposure to extreme heat during the 1980-2000 period are notstrongly correlated with several county-level covariates.

2.3 Empirical Results

Our primary analysis focuses on the effect of longer-run changes in climate on theproductivity of corn and soy, the two most important crops in the US in terms ofboth area sown and production value. The yield (production per acre) of these twocrops is the most basic measure of agricultural productivity, and is well measuredannually at the county level. However, because a focus on yields alone will not coverthe full suite of adaptations that farmers might have employed, we will examineadjustments along other possible margins.

Corn productivity

The results from our main specifications for corn yields are given in Table 2.1 andshown graphically in Figure 2.3. In our piecewise linear approach, productivity isexpected to increase linearly up to an endogenous threshold and then decrease lin-early above that threshold, and the long differences and panel models reassuringlydeliver very similar temperature thresholds (29◦C and 28◦C, respectively) and pre-cipitation thresholds (42cm and 50cm). In Columns 1-3 we run both models underthe thresholds selected by the long differences, and in Columns 4-6 we fix thresholdsat values chosen by the panel.

The panel and long differences models deliver very similar estimates of the re-sponsiveness of corn yields to temperature. Exposure to GDD below 29◦C (row 1)have small and generally insignificant effects on yields, but increases in exposure ofcorn to temperatures above 29◦ result in sharp declines in yields, as is seen in thesecond row of the table and in Figure 2.3. In our most conservative specification withstate fixed effects, exposure to each additional degree-day of heat above 29◦C resultsin a decrease in overall corn yield of 0.44%.15 The panel model delivers a slightly

15While we prefer the more conservative specifications with state fixed effects in Table 2.1, oneconcern with the inclusion of state fixed effects is that farmer responses to increasing temperaturemight vary meaningfully at the state level, for instance if governments in states that experiencedsubstantial warming helped their farmers invest in adaptation measures. These policies would beabsorbed by the state fixed effects, and could obscure meaningful adaptation measures undertakenby farmers. Our results appear inconsistent with a story of state-level adaptation to extreme heat.The effects of extreme heat in the specifications without state fixed effects (columns 1 and 4) aresubstantially more negative than in the comparable specifications with state fixed effects, which isthe opposite of what would be expected if state-level adaptation policies were an omitted variable


more negative point estimate, a -0.56% yield decline for every one degree increaseabove 29◦C, but (as quantified below) we cannot reject that the estimates are thesame. We obtain similar results when the two models are run under the temperatureand precipitation thresholds chosen by the panel model (Columns 4-6).

The estimates of the effects of precipitation on corn productivity are somewhatmore variable. The piecewise linear approach selected precipitation thresholds at 42cm (long differences) or 50 cm (panel), but most of the variation in precipitation isat values above 42 cm – e.g. the 10th percentile of annual county precipitation is41.3 cm. Long differences point estimates suggest an approximate increase in yieldsof 0.33% for each additional centimeter of rainfall above 42 cm, which are of theopposite sign and substantially larger than panel estimates. Nevertheless, we notethat even the long differences precipitation estimates remain quite small relative totemperature effects: on a growing season precipitation sample mean of 57cm, a 20%decrease (roughly the most negative climate model projection for US corn area bythe end of century) would reduce overall yields by less than 4%. As we show inSection 5, and consistent with other recent findings (Schlenker and Roberts, 2009a;Schlenker and Lobell, 2010b), any future impacts of climate change via changes inprecipitation are likely to be dominated by changes in yields induced by increasedexposure to extreme heat.

To test robustness of the corn results, we show in the remainder of this subsec-tion that our results are relatively insensitive to the choice of endpoint years, to thenumber of years used to calculate endpoints, and to an alternate estimation strategywhich further weakens our identification assumptions. In Appendix A.3, we pro-vide further evidence that our results are insensitive to the exclusion of yield andtemperature outliers, and to the inclusion of baseline covariates in the regression.

We first show that our results are largely unchanged when we change the timeperiod under study. In particular, we estimate Equation (2.10) varying T0 from 1955to 1995 in 5 year increments, and for each value of T0 we estimate 5, 10, 15, 20,25, and 30 year difference models.16 Results are shown graphically in Figure 2.4.We display the difference between the estimate of β2 for 1980-2000 (our baselineestimate) and the estimate of β2 for the period determined by the starting year anddifferencing length. The 95% confidence intervals of the differences are calculated bybootstrapping.17 The average estimate of β2 across these 39 models is -0.0058, with

in these regressions.16Some models of course could not be estimated since our data end at 2005, meaning our 5-year

smoothed estimates are only available through 2003. In each model we limit the sample to the set ofcounties from Table 2.1. Each regression is weighted by 5 year average corn area during the startingyear. The temperature and precipitation thresholds are fixed at 29◦ and 42 cm across models.

17We drew 1000 samples of 31 states with replacement and estimated all regressions for each


Figure 2.3: Relationship between temperature and corn yields.

-.06

-.04

-.02

0.0

2N

orm

aliz

ed p

redi

cted

log

yiel

ds

0 10 20 30 40Temperature (C)

LD Panel

Estimates represent the change in log corn yield under an additional day of exposure toa given ◦C temperature, relative to a day spent at 0◦C, as estimated by long differences(dark black line) and panel models (dashed grey line). The shaded area gives the confidenceinterval around the long differences estimates.


Tab

le2.

1:C

ompar

ison

oflo

ng

diff

eren

ces

and

pan

eles

tim

ates

ofth

eim

pac

tsof

tem

per

ature

and

pre

cipit

atio

non

US

corn

yie

lds

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Diff

sD

iffs

Pan

elP

an

elD

iffs

Diff

sP

an

elP

an

elG

DD

bel

owth

resh

old

-0.0

001

0.00

020.0

004∗∗∗

0.0

002∗∗

-0.0

001

0.0

003∗

0.0

005∗∗∗

0.0

003∗∗∗

(0.0

003)

(0.0

002)

(0.0

001)

(0.0

001)

(0.0

003)

(0.0

002)

(0.0

001)

(0.0

001)

GD

Dab

ove

thre

shol

d-0

.005

3∗∗∗

-0.0

044∗∗∗

-0.0

056∗∗∗

-0.0

062∗∗∗

-0.0

043∗∗∗

-0.0

037∗∗∗

-0.0

048∗∗∗

-0.0

054∗∗∗

(0.0

010)

(0.0

008)

(0.0

006)

(0.0

007)

(0.0

009)

(0.0

009)

(0.0

005)

(0.0

006)

Pre

cip

bel

owth

resh

old

0.05

15∗∗

0.02

97∗∗

0.0

118∗∗∗

0.0

095∗

0.0

253∗∗

0.0

115∗∗

0.0

068∗∗∗

0.0

057∗∗∗

(0.0

194)

(0.0

125)

(0.0

027)

(0.0

048)

(0.0

123)

(0.0

046)

(0.0

015)

(0.0

019)

Pre

cip

abov

eth

resh

old

0.00

36∗∗

0.00

34∗∗∗

-0.0

008

0.0

001

0.0

024

0.0

029∗∗∗

-0.0

018∗∗

-0.0

008

(0.0

017)

(0.0

008)

(0.0

005)

(0.0

004)

(0.0

015)

(0.0

007)

(0.0

007)

(0.0

005)

Con

stan

t0.

2655∗∗∗

0.23

97∗∗∗

3.5

721∗∗∗

4.1

872∗∗∗

0.2

674∗∗∗

0.2

400∗∗∗

3.2

423∗∗∗

3.8

577∗∗∗

(0.0

319)

(0.0

124)

(0.2

491)

(0.3

013)

(0.0

307)

(0.0

115)

(0.2

647)

(0.3

349)

Ob

serv

atio

ns

1531

1531

48465

48465

1531

1531

48465

48465

Rsq

uar

ed0.

258

0.61

00.5

90

0.8

63

0.2

43

0.6

02

0.5

93

0.8

64

Fix

edE

ffec

tsN

one

Sta

teC

ty,

Yr

Cty

,Sta

te-Y

rN

on

eS

tate

Cty

,Y

rC

ty,

Sta

te-Y

rT

thre

shol

d29

C29

C29C

29C

28C

28C

28C

28C

Pth

resh

old

42cm

42cm

42cm

42cm

50cm

50cm

50cm

50cm

Dat

aar

efo

rU

Sco

unti

esea

stof

the

100t

hm

erid

ian

,1980-2

000.

Sp

ecifi

cati

on

s1-2

an

d4-5

are

esti

mate

dw

ith

lon

gd

iffer

ence

san

d3

and

6w

ith

anan

nu

alp

anel

;se

ete

xt

for

det

ails

.S

pec

ifica

tion

s1-3

use

pie

cew

ise

lin

ear

thre

shold

sas

chose

nby

the

lon

gd

iffer

ence

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only 8 of the estimates of β2 being statistically different from our main 1980-2000estimate and none statistically different in the positive direction. This suggests ifanything that our baseline point estimate on the effect of extreme heat is conser-vative.18 We conduct an analogous exercise for the panel model to make sure thatthe effect of extreme heat in the panel does not vary with the chosen time period.Results are plotted in Figure A.8, and agree with earlier findings in Schlenker andRoberts (2009a) that the effects of inter-annual deviations in extreme heat have notdeclined significantly over time.19

Section 2.2 provided initial evidence that our “long-run” differences over timereflect substantial longer-run changes in climate rather than large short-run varia-tion around the endpoint years. To provide additional evidence that this is true, were-construct our long differences with endpoints averaged over 10 years rather than5, which should help average out idiosyncratic noise. As a further test, we utilizethe entire 1950-2005 sample, split it into 28-year periods (1950-1977 and 1978-2005),average yield and climate within each period, and then difference the period andperform our long differences estimation. We vary the sample to include any countygrowing corn in either period, or all counties growing corn in either period (or some-thing in-between). As shown in Table A.6, the effect of extreme heat is large, nega-tive, and highly significant across all specifications, and these results again suggestif anything that our baseline results conservative.

Finally, our estimates in Equation (2.9) would be biased in the presence of within-state time-varying unobservables correlated with both climate and yields. To dealwith this possibility, we use our many decades of data to construct a two periodpanel of long differences, which further weakens our identification assumption. We

sample. The differences between the 1980-2000 estimate and all other possible estimates werecalculated for each sample. The bootstrapped standard errors are the standard deviations of thedifferences in estimates.

18In Appendix Figure A.6, we display the raw coefficients and their confidence intervals for eachperiod: all estimates are negative, and in only 8 out of 39 cases to we fail to reject a significantnegative effect of extreme heat on corn productivity.

19While this unchanging sensitivity of yield to extreme heat over time could be interpretedas additional evidence of a lack of adaptation (as in Schlenker and Roberts (2009a)), we notethat whether responses to short-run variation have changed over time is conceptually distinct fromwhether farmers have responded to long-run changes in average temperature. As emphasized in ourconceptual framework, there is no reason to expect farmers to respond similarly to these two differenttypes of variation. Indeed, farmers could adapt completely to long-run changes in temperature suchthat average yields do not change – e.g. by adopting a new variety that on average performs justas well in the new expected temperature as the old variety did under the old average temperature– but still face year-to-year variation in yield due to random deviations in temperature about itsnew long-run average. As such, we view this exercise more as a test of the robustness of the panelmodel than as evidence of (a lack of) adaptation per se.


Figure 2.4: Estimates using various starting years and differencing lengths.

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estimate the following model:

∆yit = β1∆GDDit;l0:l1+β2∆GDDit;l1:∞+β3∆Precit;p<p0+β4∆Precit;p>p0+αi+δt+εit,(2.11)

where all variables are measured in 20 year differences with t indicating the timeperiod over which the difference is taken. Unobserved differences in average county-level trends are accounted for by the αi, and δt accounts for any common trendsacross counties within a given period. The β’s are now identified off within-countydifferences in climate changes over time, after having accounted for any differencesin trends common to all counties. An omitted variable in this setting would needto be a county-level variable whose trend over time differs across the two periods ina way correlated with the county-level difference in climate changes across the twoperiods, and it is difficult to construct stories for omitted variables that meet theseconditions.

In Table 2.2 we report estimates from both the 1955-1995 period and the 1960-2000 period. In all models the effect of temperature above 29◦ remains negative andsignificant even after the inclusion of county fixed effects. The main coefficients forGDD>29 are also similar to our baseline estimates in Table 2.1. The main longdifferences estimates are therefore robust to controlling for a richer set of county-specific time-varying factors.

Adaptation in corn

Comparing panel and long differences coefficients provides an estimate of recentadaptation to temperature and precipitation changes, with 1− βLD2 /βFE2 giving theshare of the short-run impacts of extreme heat that are offset in the longer run.Point estimates from Table 2.1 suggest that 22-23% of short-term yield losses fromexposure to extreme heat have been alleviated through longer run adaptations. Toquantify the uncertainty in this adaptation estimate, we bootstrap our data 1000times (sampling U.S. states with replacement to account for spatial correlation) andrecalculate 1−βLD2 /βFE2 for each iteration.20 We run this procedure for the 1980-2000period reported in Table 2.1, and repeat it for the each of the 20, 25, and 30-yearintervals shown in Figure 2.4 that start in 1970 or later.

The distribution of bootstrapped adaptation estimates for each time period areshown in Figure 2.5. Results suggest that, on the whole, longer-run adaptation to

20That is, we take a draw of states with replacement, estimate both long differences and panelmodel for those states, compute the ratio of extreme heat coefficients between the two models, savethis ratio, and repeat 1000 times for a given time period. The distribution of accumulated estimatesfor each time period is shown in Figure 2.5.


Table 2.2: The effect of climate on yields estimated with a panel of differences.

(1) (2) (3) (4)1955-1995 1955-1995 1960-2000 1960-2000

GDD below threshold 0.0008∗∗∗ 0.0007∗ 0.0004∗∗∗ 0.0003∗

(0.0003) (0.0004) (0.0001) (0.0002)

GDD above threshold -0.0066∗∗∗ -0.0058∗∗∗ -0.0031∗∗∗ -0.0023∗∗

(0.0013) (0.0020) (0.0007) (0.0010)

Precip below threshold 0.0356∗∗∗ 0.0376∗∗∗ 0.0203 0.0166(0.0079) (0.0093) (0.0135) (0.0115)

Precip above threshold 0.0017 0.0033∗ 0.0008 0.0014(0.0015) (0.0017) (0.0015) (0.0020)

Observations 2060 2060 2604 2604R squared 0.621 0.565 0.688 0.699Fixed Effects State Yr Cty Yr State Yr Cty YrT threshold 29 29 29 29P threshold 42 42 42 42

Dependent variable in all regressions is the difference in the log of smoothed corn yields. Data area two period panel with 20 year differences. Periods are 1955-1975 and 1975-1995 in Columns 1-2.Periods are 1960-1980 and 1980-2000 in Columns 3-4. The sample of counties is limited to the1980-2000 corn sample from Table 2.1. Regressions in Columns 1-2 are weighted by 1955smoothed corn acres. Regressions in Columns 3-4 are weighted by 1960 smoothed corn acres.Standard errors are clustered at the state level. Asterisks indicate statistical significance at the1% ∗∗∗,5% ∗∗, and 10% ∗ levels.

extreme heat in corn has been limited. Median estimates from each distribution allindicate that adaption has offset less than 25% of short run impacts – and pointestimates are actually slightly negative in two-thirds of the cases. In almost all caseswe can conclude that adaptation has offset at most half of the negative shorter-runimpacts of extreme heat on corn yields. Finally, all confidence intervals span zero,meaning we can never reject that there has been no more adaptation to extreme heatin the long run than has been in the short run.

Soy productivity

All of our analysis up to this point has focused on corn, the dominant field crop inthe US by both area and value. It is possible, however, that the set of availableadaptations differs by crop and there could be additional scope for adaptation withother crops. Soy is the country’s second most important crop in terms of both landarea and value of output. In Figure A.10 we show the various estimates of the effect


Figure 2.5: Percentage of the short run impacts of extreme heat on cornproductivity that are mitigated in the longer run.

−100 −50 0 50 100

% of impact offset

1970−1990

1970−1995

1970−2000

1975−1995

1975−2000

1980−2000

Combined

Each boxplot corresponds to a particular time period as labeled, and represent 1000 bootstrapestimates of 1− βLD2 /βFE2 for that time period. See text for details. The dark line in eachdistribution is the median, the grey box the interquartile range, and the whiskers representthe 5th-95th percentile. The distribution plotted at bottom represents the combination of allthe estimates in the above distributions.


of extreme heat on log soy yields as derived from the long differences model. Thehorizontal line in each panel is the 1978-2002 panel estimate of β2 for soy which is-0.0047, almost identical to the corn estimate. The thresholds for temperature andprecipitation are 29◦ and 50 cm, which are those that produce the best fit for thepanel model. While the soy results are somewhat noisier than the corn results, theaverage response to extreme heat across the 39 estimates is -0.0032, giving us a pointestimate of longer run adaptation to extreme heat of about 32%. This estimate isslightly larger but of similar magnitude to the corn estimate, and we are again unableto reject that the long differences estimates are different than the panel estimates.As for corn, there appears to have been limited adaptation to extreme temperaturesamongst soy farmers.

2.4 Alternate Explanations

Results so far suggest that corn and soy farmers are no more able to deal withincreased extreme heat exposure over the long run than they are in the short run.We now explore the extent to which this limited apparent adaptation we observe incrop yields is due to (i) measurement error, (ii) selection into or out of agriculture, (iii)adaptation along other margins, (iv) disincentives induced by existing US governmentpolicy, (v) and/or a lack of recognition that climate is changing. Evidence in favorof the first two hypotheses would challenge the validity of results; evidence in favorof any of the last three would alter their interpretation, and could make our longdifference estimates a potentially poor basis for projecting future impacts if policiesor information were to change.

Measurement error

A key concern with fixed effect estimates of the impact of climate variation is attenu-ation bias caused by measurement error in climate variables. Fixed effects estimatesare particularly susceptible to attenuation since they rely on short-term deviationsfrom average climate to identify coefficients. This makes it more difficult to separatenoise from true variation in temperature and precipitation compared to a settingwhere identification comes from relatively better-measured averages over space ortime (such as in our long differences results). Therefore one explanation for the lim-ited observed yield adaptation is simply that panel estimates are attenuated relativeto long differences estimates, and thus that that comparing the two estimates willmechanically understate any adaptation that has occurred.


We first note that because temperature and precipitation are generally negativelycorrelated, measurement error in both climate variables is likely to partially offset theattenuation caused by mis-measurement of temperature (Bound, Brown, and Math-iowetz, 2001). With more rainfall helping yields and warmer temperatures harmingthem, classical measurement error in precipitation could bias the temperature effectaway from zero: the negative correlation between temperature and rainfall resultsin warmer years having artificially low yields due to attenuation in the precipitationvariable. It is therefore not likely the case that the only effect of measurement erroron the temperature coefficients is attenuation.21

We also follow Griliches and Hausman (1986) and investigate the potential forlarge attenuation in our fixed effects estimates by comparing different panel estima-tors. If climate in a given county is highly correlated across time periods and mea-surement error is uncorrelated between successive time periods, then as Griliches andHausman (1986) show, random effects estimates should be larger in absolute valuethan the fixed effects estimates which in turn should be larger than estimates usingfirst differences. The intuition is that random effects estimates are identified usinga combination of within and between variation and therefore are less prone to mea-surement error than fixed effects estimates and first differences which rely entirelyon within-county variation. Table A.7 shows that estimates from all three estimatorsare remarkably similar, providing suggestive evidence that measurement error is notresponsible for the similarity between fixed effects and long differences estimates.

Selection

A second explanation for the observed lack of adaptation is a selection story inwhich better performing farmers exit agriculture in response to warming tempera-tures. This would leave the remaining population with lower average yields and thuscreate a mechanical negative relationship between warming temperatures and yields.Although the alternate selection story appears just as plausible – that better perform-ing farmers are more able to maintain yields in the face of climate change, and theworse performers are the ones who exit – we can check in the data whether character-istics that are correlated with productivity also changed differentially between placesthat heated and those that did not. Table A.10 provides suggestive evidence thatthis is not the case. The percentage of farms owning more than $20,000 equipment,which is positively correlated with productivity, is only weakly correlated to extreme

21This result holds so long as the measurement error for temperature and precipitation is un-correlated with the “true” temperature and precipitation values - i.e. that both exhibit classicalmeasurement error - but does not require the temperature and precipitation errors to be uncorre-lated. We have verified this via simulation, with results available upon request.


heat exposure. While this cannot fully rule out selective exit from agriculture, itprovides some evidence that selection is not driving our yield results.

Adaptation along other margins

A third explanation is that a focus on corn and soy yields, while capturing many of theoff-mentioned modes of adaptation (e.g. switching seed varieties), might not captureall possible margins of adjustment available to farmers and thus could understatethe extent of overall adaptation to climate change.

One way to capture broader economic adjustment to changes in climate is toexplore climate impacts on farm revenues or profits, an approach adopted in some ofthe recent literature (e.g. Deschenes and Greenstone (2007)). There are at least twoempirical challenges with using profits in particular. The first is that measures ofrevenues and expenditures are only available every 5 years when the US AgriculturalCensus is conducted. Given that our differencing approach seeks to capture changein average farm outcomes over time, if both revenues and costs respond to annualfluctuations in climate, then differencing two “snapshots” from particular years mightprovide a very noisy measure of the longer term change in profitability. A secondconcern is that available data on expenses do not measure all relevant costs (e.g. thevalue of own or family labor on the farm), which might further bias profit estimatesif these expenses also respond to changes in climate. As shown in Appendix SectionA.7, long differences regressions with such a measure of “profit” as the dependentvariable are indeed very noisy, and we cannot reject that there is no effect on profits,and similarly cannot reject that the effect of extreme heat on profits is a factor of 3larger (and more negative) than the effect on corn yields – i.e. that each additionalday of exposure to temperatures above 29C reduced annual profits by 1.4%. Thisdoes not provide much insight on the relationship between extreme heat exposureand profitability.

We take two alternate approaches to exploring impacts on economic profitability.The first is to construct an annual measure of revenue per acre, which we do bycombining annual county-level yield data with annual data on state-level prices.22 Wethen sum these revenues across the six major crops grown during the main Spring-Summer-Fall season in our sample counties: corn, soy, cotton, spring wheat, hay,and rice. This revenue measure will underestimate total revenue to the extent thatnot all contributing crops are included, but should capture any gain from switchingamong these primary crops in response to a changing climate. It will also capture

22Prices are only available at the state level and to our knowledge do not vary much withinstates within a given year.


any offsetting effect of price movements caused by yield declines, which while not anadaptation measure per se might reduce the need for other adaptation. Our secondapproach proceeds with the available expenses data from the Census to examine theimpact of longer-run changes in climate on different input expenditures.23

Table 2.3 shows results for our revenue measures. Consistent with some offsettingprice movements, point estimates on how corn revenues per acre respond to extremeheat are slightly less negative than yield estimates under both panel and long differ-ences models (Columns 1 and 2), but at least for the differences model we cannotreject that the coefficients are the same as the yield estimates. Revenues for thesix main crops appear roughly equally sensitive to extreme heat in a panel and longdifferences setting (Columns 3 and 4), again suggesting that longer run adaptationhas been minimal.24 Furthermore, we show in Table A.8 that trends in climate havehad minimal effects on expenditures on fertilizer, seed, chemical, and petroleum. Weinterpret this as further evidence that yield declines are not masking other adjust-ments that somehow reduce the economic losses associated with exposure to extremeheat.

To further explore whether our yield estimates hide beneficial switching out ofcorn and to other crops, we repeat our long differences estimation with changes in(log) corn area and changes in the percentage of total farmland planted to corn asdependent variables. Results are given in Table 2.4, and we focus on the sample ofcounties with extreme heat outliers trimmed.25 There appears to have been minimal

23We attempt to capture changes in average expenditures by averaging two census outcomesnear each endpoint and then differencing these averaged values. For example, ag census data areavailable in 1978, 1982, 1987, 1992, 1997, and 2002. The change in fertilizer expenditures over theperiod are constructed as: ∆fertilizer expenditure1980−2000 = (fert1997 + fert2002)/2 - (fert1978 +fert1982)/2

24Coefficient estimates on the six-crop revenue measure are nevertheless about half the size ofestimates for corn. We do not interpret this as evidence for adaptation for two reasons. First, paneland long differences estimates for how crop revenues respond to extreme heat are the same. Second,adaptation-related explanations for why crop revenues should be less sensitive than corn revenue– e.g. farmers switch among crops to optimize revenues – would require that farmers are able toadjust their crop mix on an annual level in before any extreme heat for that season is realized.This seems unlikely. We believe a more likely explanation is that we are more poorly measuring theclimate variables and thresholds that are relevant to these other crops; regressions are run under thecorn temperature and precipitation thresholds, and using data based on the corn growing season.If climate is measured with noise, then coefficient estimates will be attenuated.

25As shown in Table A.5 - and unlike for our yield outcomes - a few outcomes in this tableare altered fairly substantially when these five outliers (0.3% of the sample) are included. Giventhat these counties are all geographically distinct (along the Mexico border in southern Texas),and experienced up to 20 times the average increase in exposure to extreme heat than our mediancounty in the sample, it seems reasonable to exclude them from the analysis.


Table 2.3: Effects of climate variation on crop revenues

Corn Main Spring Crops

(1) (2) (3) (4)Panel Diffs Panel Diffs

GDD below threshold 0.0005∗∗∗ 0.0003 0.0002 0.0003(0.0001) (0.0002) (0.0001) (0.0003)

GDD above threshold -0.0046∗∗∗ -0.0042∗∗∗ -0.0024∗∗∗ -0.0023∗∗

(0.0005) (0.0009) (0.0003) (0.0011)

Precip below threshold 0.0068∗∗∗ 0.0107∗∗ 0.0058∗∗∗ 0.0116∗

(0.0016) (0.0048) (0.0014) (0.0058)

Precip above threshold -0.0014∗∗ 0.0035∗∗∗ -0.0012∗∗ 0.0016(0.0007) (0.0010) (0.0005) (0.0016)

Constant 3.9556∗∗∗ -0.0116 4.7926∗∗∗ 0.0121(0.2539) (0.0122) (0.3619) (0.0210)

Observations 48465 1516 48465 1531Mean of Dep Variable 5.55 -0.01 5.36 0.03R squared 0.568 0.579 0.490 0.454Fixed Effects Cty, Yr State Cty, Yr State

In Columns 1 and 2 the dependent variable is log of agricultural revenue per acre from corn.Dependent variable in Columns 3 and 4 is log of agricultural revenue per acre from 6 main cropsgrown during the spring season (corn, soy, cotton, spring wheat, hay, and rice). Revenuescalculated as yield per acre multiplied by state-level annual prices. Panel regressions are weightedby average area cultivated to corn (Column 1) and main crops (Column 3) from 1978-2002. Longdifferences regressions are weighted by smoothed corn area in 1980 (Column 2) and smoothed areacultivated to main crops (Column 4). Temperature threshold is 28 and precipitation threshold is50 in all regressions. Standard errors are clustered at the state level. Asterisks indicate statisticalsignificance at the 1% ∗∗∗,5% ∗∗, and 10% ∗ levels.

impact of increased exposure to extreme heat on total area planted to corn (Column1), but we do find some evidence that the percentage of total farm area planted tocorn declined in areas where extreme heat exposure grew. This effect appears small.In counties where increases in extreme heat were the most severe, observed increasesin GDD above 29◦C would have reduced the percentage of area planted to corn byroughly 3.5%.

A final adaptation available to farmers would be to exit agriculture altogether, anoption that recent literature has suggested is a possibility. For instance, Hornbeck(2012a) shows that population decline was the main margin of adjustment acrossthe Great Plains after the American Dust Bowl. Feng, Oppenheimer, and Schlenker


(2012a) use weather as an instrument for yields to show that declines in agriculturalproductivity in more recent times result in more outmigration from rural areas of theCorn Belt. To quantify adaptation along this margin, we repeat our long differencesestimation with total farm area, total number of farms, and county population asdependent variables. If there is a net reduction in the number of people farmingdue to increased exposure to extreme heat, we should see a decline in the number offarms; if this additional farmland is not purchased and farmed by remaining farmers,we should also see a decline in total farmland.

Results are in Columns 3-5 of Table 2.4. Point estimates of the effect of ex-treme heat on both (log) farm area and number of farms are negative but small andstatistically insignificant. Nevertheless, the standard error on the number of farmsmeasure is such that we cannot rule out a 5-10% decline in the number of farms forthe counties experiencing the greatest increase in exposure to extreme heat over ourmain sample period.26 Point estimates on the response of population to extreme heatexposure are similar to estimates for number of farms, and again although estimatesare not statistically significant we cannot rule out population declines of 5-10% forthe counties that warmed the most. Taken together, and consistent with the recentliterature, these results suggest that simply not farming may be an immediate adap-tation to climate change for some farmers – although we have little to say on thewelfare effects of such migration.

Policy disincentives to adapt

A fourth explanation for limited adaptation is that certain governmental agriculturalsupport programs – subsidized crop insurance in particular – could have reducedfarmers’ incentives to adapt. In the crop insurance program, the federal govern-ment insures farmers against substantial losses while also paying most or all of theirinsurance premiums, and this plausibly could have reduced farmers’ incentives toundertake costly adaptations.27

26As an alternate approach, and to address any concern that exiting agriculture is a particu-larly slow process, we adopt a strategy similar to Hornbeck (2012a) and examine how the numberof farmers in the 1980’s and 1990’s responded to variation in warming during the 1970s. Pointestimates indicate small but statistically significant reductions in the number of farms followingearlier exposure to extreme heat, again suggesting that simply not farming may be an immediateadaptation to climate change for some farmers.

27For more details on the program, see http://www.rma.usda.gov/. We note that direct incomesupport from the government constitutes a rather small percentage of cash income during our mainstudy period – an average of 7% in the Corn Belt during the 1980-2000 period – suggesting thatthe distortionary effects of these programs on adaptation decision were likely small. Additionaldata on farm income over time are available here: http://www.ers.usda.gov/data-products/farm-


Table 2.4: Effects of climate variation on alternate adjustment margins

(1) (2) (3) (4) (5)Corn area Corn share Farm area Num. farms Population

GDD below threshold 0.0010 0.0003∗∗∗ -0.0001 -0.0002 0.0006∗∗

(0.0012) (0.0001) (0.0001) (0.0002) (0.0003)

GDD above threshold -0.0005 -0.0009∗∗ 0.0000 -0.0007 -0.0008(0.0038) (0.0004) (0.0004) (0.0010) (0.0015)

Precip below threshold 0.0264 -0.0004 0.0037 0.0021 -0.0236∗∗

(0.0637) (0.0034) (0.0035) (0.0029) (0.0106)

Precip above threshold -0.0051 -0.0016 0.0007 -0.0013 0.0047∗

(0.0063) (0.0010) (0.0007) (0.0033) (0.0024)

Constant -0.0130 -0.0174∗∗∗ -0.0614∗∗∗ -0.1836∗∗∗ 0.0144(0.0687) (0.0045) (0.0075) (0.0157) (0.0160)

Observations 1511 1516 1523 1526 1526Mean of Dep Variable 0.075 0.002 -0.068 -0.202 0.045R squared 0.645 0.418 0.399 0.488 0.392Fixed Effects State State State State StateT threshold 29 29 29 29 29P threshold 42 42 42 42 42

Dependent variable is difference in log of corn acres (Column 1), difference in share of agriculturalarea planted to corn (Column 2), difference in total log farm area (Column 3), difference in lognumber of farms (Column 4), and difference in log county population (Column 5). All regressionsare long differences from 1980-2000, with the sample trimmed of extreme outliers in thetemperature data. All regressions are weighted by average agricultural area from 1978-2002.Standard errors are clustered at the state level. Asterisks indicate statistical significance at the1% ∗∗∗,5% ∗∗, and 10% ∗ levels.

As one check on whether observed lack of adaptation is being driven by theexistence of subsidized insurance, we utilize the large-scale expansion of the federalcrop insurance program in the mid-1990s and compare the impact of long-run changesin temperature before and after the expansion. This expansion, related to a set ofrevised government policies that were instated beginning in 1994, roughly tripledparticipation in the crop insurance program relative to the late 1980s, and by theend of our study period over 80% of farmers were participating in the program. Wefind that the effects of temperature in the post-expansion period were the same oreven slightly smaller (in absolute value) than the effects in the pre-expansion period,which is the opposite of what would be expected if subsidized insurance had reduced

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farmers’ incentive to adapt.28 While this is not a perfect test – other things couldhave changed over time that affected farmers ability to adapt – it provides suggestiveevidence that our results are not being wholly driven by government programs.

Lack of recognition of climate change

Finally, it could be the case that farmers didn’t adapt because they didn’t realizethe climate was changing and that adaptation was needed. Although this doesn’taffect the internal validity of our results, it could mean that our results might pro-vide a poor guide to impacts under future climate change if the need for adaptationbecomes apparent. Unfortunately we do not directly observe farmer perceptions oftemperature increases, nor their knowledge of the relationship between temperatureand crop yields.29 To make progress, and building directly on the model presented inSection 2, we first explore whether farmers’ responsiveness is function of character-istics that likely shape their ability to learn about a changing climate. In particular,if adaptation is limited by a difficulty in learning about climate change, then weshould observe more adaptation when farmers are given more time to learn abouta given change in climate, and more adaptation if they are in an area with a lowertemperature variance and thus a clearer “signal” of a given change in climate.

Our data are inconsistent with either of these prediction. First, as shown inFigure 2.4, point estimates for longer long-difference periods (e.g. the 25- and 30-year estimates in the bottom right panels) are almost uniformly more negative thanestimates for the 1980-2000 period, although we cannot reject that they are the samein most cases. Second, we find little evidence that a lower temperature variance atbaseline increased adaptation to a subsequent temperature increase. In the firstcolumn of Table 2.5, we re-estimate our main equation, interacting the 1980-2000extreme temperature change in a given county with the baseline (1950-1980) variance

28Running the long differences model for 1997-2003 (thus, with 5-yr average endpoints, utilizingdata from 1995-2005) gives a βGDD>29 = -0.00438 (SE = 0.00179), which is almost exactly equalto our baseline estimate for the 1980-2000 period, and less negative than the coefficient for the longdifferences run over 1980-1993 (βGDD>29 = -0.0056)

29A few existing surveys do ask farmers about their perceptions of different aspects of climatechange, but the results are difficult to interpret. For instance, although Iowa is one of the stateswhere temperature has changed the least in recent years, 68% of Iowa farmers in a recent surveyindicated that they believe that “climate change is occurring” (Iowa State Extension Service, 2011),but only 35% of them were concerned about the impacts of climate change on their farm operation.Similarly, only 18% of North Carolina farmers believed that climate change will decrease averageyields by at least 5% over the next 25 years (Rejesus, 2012), but slightly less than a 5% declineby 2030 could be consistent with projected impacts under more conservative warming scenarios,meaning these responses do not necessarily suggest a distorted perception of climate change.


in extreme heat exposure in that county. The estimate on the interaction term issmall and statistically insignificant, providing little evidence that a lower underlyingvariance helped farmers separate signal from noise. As a third check, and following onrecent survey evidence suggesting that past experience informs current beliefs aboutclimate change30, we explore whether counties that were rapidly warming prior to ourstudy period were more adaptive during our study period. In particular, we allow theeffect of extreme heat over the 1980-2000 period in a given county to depend on thechange in extreme heat in that county during the period from 1960-1980, or during1970-80 (if farmers weight recent evidence more heavily). As shown in Columns 2and 3 of Table 2.5, coefficients on either interaction are small and insignificant, andonly the coefficient on the 1960-80 interaction has the expected sign.

As an additional check on the role of beliefs in shaping adaptation, we exploit thefact that beliefs about climate change display well known heterogeneity by politicalparty affiliation, with Republicans consistently less likely than Democrats to believethat climate change is occurring (e.g. Dunlap and McCright (2008)). We re-estimateour main equation and include an interaction between our climate variables andGeorge W. Bush’s county-level vote share in the 2000 presidential election. Becausepublic debate and awareness about climate change begin in earnest in the late 1980’sand early ‘90’s, this is a reasonable – if highly imperfect – proxy for beliefs aboutclimate change. Results are given in Column 5 of Table 2.5, and again suggest thatexpectations about climate change, as proxied by political beliefs, had a minimaleffect on the responsiveness of farmers to extreme heat exposure: more Republicancounties were if anything less sensitive to extreme heat exposure over the studyperiod.

A final possibility is that adaptation is limited not by farmers’ difficulty in learn-ing about changing climate, but instead by difficulty in learning about the productionfunction with respect to climate – in particular, learning that extreme heat can bedamaging to productivity. Although this is a different type of learning, it suggestssimilar empirical tests as before: farmers should have been more likely to learn aboutthe production function had they been given more time to do so, or had they beenexposed to extreme heat in a previous period. As just discussed, we find little evi-dence that either of these predictions is true. This remains the case when we expandthe latter prediction to include the possibility that counties could learn from othernearby counties’ experiences, interacting county-level changes in extreme heat over1980-2000 with state-level changes in extreme heat over the previous period (column4 of Table 2.5). As an alternate check, and building on existing evidence that higher

30For instance, Myers et al. (2012) and Howe et al. (2012) show that persons residing in areasthat have warmed in recent history are more likely to believe in future climate changes.


educational achievement accelerates learning about agricultural technologies (Feder,Just, and Zilberman, 1985), we allow the effect of extreme heat to vary by county-level educational attainment using data on county-level high school graduation ratesfrom the 1980 US Census. As shown in Column 6 of Table 2.5, we find little evidencethat county-level educational attainment affected subsequent adaptation.

Finally, as indirect evidence that farmers did recognize that changes in climatewere shaping productivity during our study period, we study whether uptake ofgovernment crop insurance varied as a function of changing exposure to extremeheat. Although premiums in the crop insurance program are very highly subsidized,meaning that farmers might purchase insurance regardless of the amount of risk theyface, the average percent of corn acreage covered by these insurance programs by theend of our study period was “only” 80% (with some counties below 40%), suggestingthat there remained some variation in insurance purchases.

To see whether insurance take-up responded to our observed climate trends, were-estimate our long-differences model using insurance adoption at the end of ourstudy period (i.e. a 5-year average over 1998-2002) as the dependent variable. Weexplore four measures of take-up: the percent of corn acreage in a county enrolled inany of the multiple crop government crop insurance programs, the log of acres en-rolled in a county, the number of policies sold in each county, and the total premiumspaid (including subsidies) in each county. Results from this exercise are shown inTable A.11. While the coefficients on the temperature variables are only sometimessignificant with state-level clustering, results suggest that participation in the gov-ernment insurance program by 2000 was higher in counties who saw large increases inexposure to harmful temperatures (GDD>29C) over the previous two decades, andlower in counties that saw increase in exposure to generally helpful temperatures(GDD0-29C) over the same period. Moving from the 10th to the 90th percentile ofthe distribution of GDD>29C changes implies roughly a 5ppt increase in the acreageinsured, a 23% increase in the number of policies sold, and a 20% increase in thetotal premiums paid. Again, however, only one of these estimates is significant atconventional levels with state-level clustering, so we do not wish to over-sell theseresults.

Taken as a whole, then, we find little evidence that farmers who were morelikely to learn about the effects of extreme heat on yields, or farmers who weremore likely to update their expectations about future exposure to extreme heat,were more able to adapt to subsequent extreme heat exposure. This implies thatthe lack of observed adaptation is not fully explained by a lack of recognition thatthe climate was changing for the worse, and indeed we do find some evidence thatchanges in climate were in fact being recognized. Thus insofar as farmers recognized

CHAPTER 2. ADAPTATION TO CLIMATE IN US AGRICULTURE 38T

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the warming trend for what it was but had few adaptation options to exploit, thenusing these observed responses to warming to project future climate change impactsappears a reasonable “business-as-usual” approach. Nevertheless, because we cannotdefinitively rule out that past responses were affected by imperfect recognition ofclimate and its effects, and because farmers might more effectively learn about thesethings in the future, these caveats must be kept in mind when interpreting ourprojections.

2.5 Projections of impacts under future climate

change

Our final empirical exercise is to build projections of the impacts of future climatechange on agricultural outcomes in the US. To do this we combine estimates ofclimate sensitivities from our long differences approach with projections of futurechanges in temperature and precipitation derived from 18 global climate modelsrunning the A1B emissions scenario. Using data from the full ensemble of availableclimate models is important for capturing the range of uncertainty inherent in futureclimate change (Burke et al., 2013). Details of the emissions scenario, the climatemodels, and their application are provided in the Appendix.

The overall purpose of these projections is to provide insight into potential im-pacts under a “business-as-usual” scenario in which the future world responds tochanges in climate similarly to how it has responded in the past. While it is un-knowable whether future responses to climate will in fact resemble past responses –farmers could adapt production practices in previously unobserved ways, or couldmove crop production to entirely new areas – our long differences approach offerstwo advantages over existing projections. First, the range of long-run changes inclimate projected by climate models through mid-century is largely contained in therange of long-run changes in climate in our historical sample, meaning our projec-tions are not large extrapolations beyond past changes. Second, our estimates betteraccount for farmers’ recent ability to adapt to longer-run changes in climate, rela-tive to typical panel-based projections that use shorter-run responses in the past toinform estimates of longer-run responses in the future.

In Figure 2.6 we present projections of average annual changes in corn yield by2050 across the 18 climate models. In the top panel we use long differences estimatesto generate predictions from precipitation changes, temperature changes, and com-bined effects of changing both temperature and precipitation. The most substantialnegative effects of climate change are driven by increases in temperature, and while


the magnitude of the negative effects of temperature vary across climate models,all predict fairly substantial negative effects of future warming on corn productivity.For instance, under climate change projections from the commonly used Hadley CM3climate model, our long differences estimates deliver a predicted decrease in yields ofapproximately 27.3% relative to a world that did not experience climate change. Themagnitude of this projection is similar to the projections from fixed effects estimatesin Schlenker and Roberts (2009a).

The bottom panel of the figure compares projections from long difference andpanel models for each of the 18 different climate models. The similarity of regressionestimates in the historical data results in projections that are comparable for bothlong differences and fixed effects, although the long differences estimates are some-what noisier. We note that this noise is almost entirely due to the coefficient andstandard error on GDD below 29C, which is much less precisely estimated in thelong differences than in the panel. Since a given temperature rise increases exposureto both harmful and beneficial GDD for almost all counties in our sample, the noisein the GDD below 29C estimate greatly expands the confidence interval on the longdifferences projections.

Nevertheless, net of any adaptations that farmers have employed in the past, themedian climate model projects average yield declines of 15% by mid-century, withsome models projecting yield losses as low as 7% and others losses as high as 64%.To put these projected losses in perspective, the 2012 drought and heat wave thatwas considered one of the worst on record and that received extensive attention inthe press decreased average corn yields for the year by 15-20% relative to the priorfew years.31 Our median projection suggests that by 2050, every year will experiencelosses this large. Valued at production quantities and prices averaged over 2006-2010for our sample counties, 15% yield losses would generate annual dollar losses of $6.7billion by 2050.

2.6 Conclusions

Quantitative estimates of the impacts of climate change on various economic out-comes are an important input to public policy, informing decisions about investmentsin both emissions reductions and in measures to help economies adapt to a changingclimate. A common concern with many existing impact estimates is that they donot account for longer-run adjustments that economic agents might make in the faceof a changing climate. These studies typically rely on short-run variation in weather

31As estimated by the Oct 11th 2012 version of the seasonally-updated USDA forecast, availableat http://www.usda.gov/oce/commodity/wasde/


Figure 2.6: Projected impacts of climate change on corn yields by 2050.

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Top panel: impacts as projected by the long differences model, for each of the 18 climatemodels reporting the A1B (“business as usual”) climate scenario. Circles represent pro-jection point estimates, whiskers the 95% CI, and colors represent projections using onlyprecipitation changes (blue), temperature changes (black), or both combined (red). Projec-tions are separately for each climate model, as labeled. Bottom panel: projected impacts ofcombined temperature and precipitation changes across the same climate models, based onlong differences (red) on panel estimates (black) of historical sensitivities to climate. Themedian projection is shown as a dashed line.


to estimate how outcomes respond to temperature and precipitation changes, anapproach that helps solve identification problems but that might fail to capture im-portant adjustments that agents can make in the longer-run.

We exploit large variation in multi-decade changes in temperature and precip-itation across US counties to estimate how farmers have responded to longer-runchanges in climate. We argue that these changes are plausibly exogenous and showthat their magnitude is on par with future changes in climate projected by global cli-mate models, making them an ideal source of variation to identify historical responsesto longer-run changes in climate and in turn to project future impacts.

We show that the productivity of the two main US crops, corn and soy, respondedvery negatively to multi-decadal changes in exposure to extreme heat. These esti-mates of longer-run responses are indistinguishable from estimates of how the samecrops responded to short-run (annual) variation in extreme heat over the same pe-riod, suggesting that farmers were no more able to mitigate the negative effects ofclimate in the long run than they were in the short run. This apparent lack of adap-tation does not appear to be driven by any of a variety of alternative explanations:fixed effect estimates do not appear substantially attenuated relative to long differ-ences estimates, results do not appear to be driven by time-trending unobservables,and farmers do not appear to be adapting along other margins within agriculture.We also provide evidence that this lack of adaptation was not driven by a lack ofrecognition that climate was changing, perhaps suggesting that farmers either lackedadaptation options or found them too expensive to exploit.

Using climate change projections from 18 global climate models, we project po-tential impacts on corn productivity by mid-century. If future adaptations are aseffective as past adaptations in mitigating the effects of exposure to extreme heat,our median estimate is that future climate change will reduce annual corn productiv-ity in 2050 by roughly 15%, which is on par with the effect of the highly-publicized“extreme” drought and heat wave experienced across the US corn belt in the summerof 2012. Given that these projections account for farmers’ present adaptive abilities,our results imply substantial losses under future climate change in the absence ofefforts to help farmers better adapt to extreme heat.

43

Chapter 3

Climate, economic shocks, andHIV in Africa

3.1 Introduction*

The relationship between income and health has long been of interest to economists,and a lengthy literature documents strong linkages between economic conditionsand many important health outcomes (e.g. Currie, 2009). There has been muchless progress, however, in understanding the economic foundations of the HIV/AIDSepidemic, one of the most important global health challenges. Such an understandingmight yield particular dividends in sub-Saharan Africa (SSA), where over a millionpeople continue to become newly infected with the disease each year (UNAIDS,2010).

In this paper we explore the role of negative income shocks in shaping the evolu-tion of the HIV/AIDS epidemic in Africa. Such shocks represent a well-documentedchallenge to poor households around the world. Lacking access to formal savings andinsurance, income shortfalls often force poor households to make difficult tradeoffsbetween short-run consumption and longer-run earnings and human capital accumu-lation (Rosenzweig and Wolpin, 1993; Ferreira and Schady, 2009; Maccini and Yang,2009). Recent indirect evidence suggests that variation in income could also affectimportant disease outcomes, either by altering individual sexual behavior (Bairdet al., 2012; Kohler and Thornton, 2012; Robinson and Yeh, 2011b), or by affectingother phenomena such as migration or marriage timing that play a documented rolein disease transmission (Lurie et al., 2003; Clark, 2004; Oster, 2012). Were income

*This chapter is from work co-authored with Erick Gong and Kelly Jones, entitled “Incomeshocks and HIV in Africa”.

CHAPTER 3. CLIMATE, ECONOMIC SHOCKS, AND HIV IN AFRICA 44

variation to play a role in HIV outcomes through any of these mechanisms, it wouldsuggest that addressing income risk could play an important role in comprehensiveHIV prevention strategies.1

Using one of the most widespread sources of income variation in the developingworld – rainfall-related shocks to agriculture – we directly assess the effect of negativeincome shocks on HIV outcomes across the African continent. We use the exogenoustiming of rainfall events to develop an annual measure of shocks that is orthogonalto time-invariant determinants of disease outcomes. Our definition of a shock isannual rainfall below the 15th percentile of the historical distribution of rainfall for alocal area. Using data on roughly two-hundred thousand individuals across nineteenAfrican countries, we compare the HIV status of individuals randomly exposed to ahigher number of recent shocks (past 10 years) to the status of nearby individualsexposed to fewer recent shocks.

We find that exposure to recent negative rainfall shocks substantially increasesHIV infection rates in rural areas with high baseline HIV prevalence. Exposure to asingle additional shock leads to a significant 11% increase in overall HIV infection.These results are robust to a variety of ways of constructing the shock measure, to avariety of controls, and to a set of placebo tests. Consistent with expectations, we findlittle effect of shocks in urban areas (where incomes should be less sensitive to rainfall)and in low-prevalence regions (where there exists less HIV to be transmitted).

We show that these individual-level results are mirrored in the broader cross-country patterns of HIV prevalence observed in SSA. Using country-level data fromUNAIDS, we show that exposure to shocks at the country level is also associatedwith significantly higher levels of HIV infection, and that our shock measure explains14-21% of the cross-country variation in HIV prevalence across SSA. This providessomewhat independent evidence on the role of shocks in shaping HIV outcomes, andimplies that meteorological bad luck earlier on in the AIDS epidemic could haveplayed a substantial role in shaping how the epidemic progressed over the followingdecades.

While these reduced form results provide direct causal evidence that negativeshocks substantially increase equilibrium HIV infection rates, they provide limitedinsight into the many channels through which shocks might shape HIV risk. Forinstance, adults may respond to shocks by temporarily migrating in search for work(Skoufias, 2003), or school-aged girls may respond by marrying at an earlier age toincrease economic security (Jensen and Thornton, 2003), behaviors that are bothassociated with an increased risk for HIV (Lurie et al., 2003; Clark, 2004). Alterna-

1Economic interventions such as formal insurance could compliment existing biomedical inter-ventions such as male circumcision and ARV treatment as prevention.


tively, women may increase their sexual activity in response to economic hardshipin order to obtain transfers (both monetary and in-kind) from their male partners(LoPiccalo, Robinson, and Yeh, forthcoming; Swidler and Watkins, 2007; Robinsonand Yeh, 2011b; Dinkelman, Lam, and Leibbrandt, 2008). This “transactional sex”has been documented among women who are not commercial sex workers in nu-merous African countries and is believed to be a key driver in the AIDS epidemic(UNAIDS, 2010), a fact that has motivated numerous recent attempts to address thelink between income and sexual behavior through cash transfers (Baird, McIntosh,and Ozler, 2011; Handa et al., 2012; Kohler and Thornton, 2012; de Walque et al.,2012).

While we are unable to definitively isolate the mechanism by which shocks in-crease HIV, we show that our data are largely inconsistent with either a migration oran early-sexual-debut explanation. In particular, we show that shocks do not induceearlier marriage or increased time away from one’s village. Furthermore, we showthat the effects of shocks on HIV are larger for men working outside of agriculture(whose purchasing power would have declined the least), evidence that is broadlyconsistent with an outward shift in the supply of transactional sex.

This work contributes to the literature within and outside of economics thatseeks to understand why the AIDS epidemic has disproportionately affected sub-Saharan Africa. Our results provide strong evidence that a primary source of incomevariation for rural Africans – rainfall-related variation in agricultural productivity– could be an important contributing factor to the epidemic. These results suggestthat economic conditions play a significant role in the AIDS epidemic in SSA, andare related to previous work using macro-level data to explore the effects of economicgrowth on the AIDS epidemic (Oster, 2012).

We also contribute to a broader body of work on the health and livelihood conse-quences of income shocks. A host of papers show that when saving is difficult and in-surance incomplete, negative income shocks can have seriously detrimental effects onlonger-run livelihood outcomes. In contrast to existing work, we identify behavioralresponses that are not only detrimental to an individual’s or household’s wellbeingbut that also generate large negative health externalities for the community. As such,our results add further impetus to the growing effort aimed at increasing access torisk management tools in the developing world, and could suggest a role for publicsubsidy if the negative health externalities brought on by incomplete insurance areas large as we estimate.

The rest of the paper is organized as follows. In section 3.2 we present a sim-ple conceptual framework to motivate our empirical approach. Section 3.3 presentsthe data and our empirical methods. Section 3.4 discusses our main results and ro-bustness checks, and section 3.5 seeks evidence of behavioral pathways. Section 3.6


explores how these effects scale up to the country level. Finally, section 3.7 discussespolicy implications and concludes.

3.2 Conceptual Framework

The goal of this paper is to understand how economic conditions shape HIV risk. Ourempirical approach examines how a plausibly exogenous source of income variation– exceptionally low rainfall realizations at a given location relative to long-termaverages (“shocks”) – affects local HIV outcomes. Our primary result establishesa strong positive relationship between these shocks and local HIV prevalence. Weargue that this is a causal relationship because our shock measure is, by construction,uncorrelated with other time-invariant factors that might also affect disease outcomes(see further discussion in section 3.3). Here we discuss why rainfall-related shocksmight matter for HIV, and use this discussion to generate predictions of where andfor whom the reduced form relationship between drought and HIV should be largest.

Our empirical analysis begins by examining the reduced-form relationship be-tween drought-related shocks (S) and HIV infection, or ∂HIV

∂S. Define p as a measure

of sexual risk, and z as income. The reduced form relationship between droughtshocks and HIV can then be written as:

∂HIV

∂S=∂HIV

∂p

∂p

∂z

∂z

∂S(3.1)

The three terms on the right hand side are the following:

• ∂HIV∂p

represents the relationship between HIV infection and sexual risk. Inthe sub-Saharan African setting, heterosexual sex is the primary driver of theepidemic (UNAIDS, 2010), and so deviations in the path of the epidemic aredriven largely by changes in sexual behavior. The risk of HIV infection isincreasing in risky sexual behavior such as having multiple concurrent partners

or unprotected sex(∂HIV∂p

> 0)

(Halperin and Epstein, 2008; Potts et al., 2008;

Stoneburner and Low-Beer, 2004; Epstein, 2007). Importantly, this relationshipalso depends on the prevalence of HIV in an area (λ). Regions with higher HIVprevalence will have a stronger relationship between sexual behavior and newinfections than regions with low prevalence ∂HIV

∂p∂λ> 0.

• ∂p∂z

represents the impact of a deviation in income on sexual risk (p). A growingliterature documents the importance of economic factors in shaping sexual riskin Africa (Baird et al., 2012; Kohler and Thornton, 2012; Robinson and Yeh,


2011b). Sexual risk can be measured as the number of partners and/or numberof unprotected sexual acts, but can also be measured by how likely a partneris infected with HIV. In section 3.5 we discuss several ways identified by theliterature by which shortfalls in income might alter sexual behavior, all of whichsuggest a negative relationship between an income deviation and sexual riskfor at least some subset of the population (i.e. ∂p

∂z< 0). Such mechanisms can

broadly be considered coping behaviors in response to income shocks, and willbe operative for different subsets of the population depending on the copingmechanism in question.

• Finally, ∂z∂S

is the relationship between negative rainfall shocks and incomeshocks. As is frequently recognized in the literature, and as we demonstrate inappendix B.2, variation in rainfall generates substantial variation in both agri-cultural productivity and broader income measures in Africa. We expect thatin rural areas (r), where most income is generated from rain-fed agriculture,rainfall shocks will have a larger (negative) effect on income than in urban areas

where agriculture is less important for the local economy(∂zr∂Sr

< ∂zu∂Su≤ 0)

.

Because there is little disagreement in the literature on the signs of the first andthird terms in Equation 3.1, the overall sign of ∂HIV

∂Swill depend on how sexual risk

responds to variation in income. If we assume that this term is non-zero, then twoimmediate predictions are generated from Equation 3.1.

• The effect of shocks on HIV will be larger (in absolute value) where baselineprevalence λ is higher. Intuitively, if shocks increase HIV through changes insexual behavior, the effect of shocks will be amplified in places where there ismore HIV to transmit.

• The effect of shocks on HIV will be larger (in absolute value) in rural areaswhere income is more dependent on agriculture (and therefore on rainfall).

The sign of ∂p∂z

will determine the overall sign of ∂HIV∂S

. If some segment of thepopulation copes with negative income shocks in a way that increases sexual risk, asis suggested by the literature, then Equation 3.1 indicates that the overall relationshipbetween HIV and shocks for these populations would be positive, ∂HIV

∂S> 0.


3.3 Empirical Methods

Individual HIV-status data

Our individual-level data are taken from 21 Demographic and Health Surveys (DHS)conducted in 19 different Sub-Saharan countries.2 Of the existing DHS surveysavailable in early 2011, we employ all those that include results from individual-levelHIV-tests as well as longitude and latitude information on the individual’s location,allowing us to map households to data on shocks.3 For two countries (Kenya andTanzania), two survey rounds matched these criteria; however, these are separatecross-sections and creation of panel data at the individual or cluster level is notpossible. Nonetheless, for each country both rounds are included in the analysis asentirely separate surveys.4

Each of these surveys randomly samples clusters of households from stratifiedregions and then randomly samples households within each cluster. In each sampledhousehold, every woman aged 15-49 is asked questions regarding health, fertility, andsexual behavior.5 A men’s sample is composed of all men within a specified age rangewithin households selected for the men’s sample.6 Depending on the survey, this iseither all sampled households, or a random half (or third) of households within eachcluster. Details regarding survey-specific sampling are presented in Appendix TableB.1. In all households selected for the men’s sample, all surveyed men and women areasked to provide a finger-prick blood smear for HIV-testing.7 By employing cluster-specific inverse-probability sampling weights, the HIV prevalence rates estimatedwith this data are representative at the national level.8

Table 3.1 gives the list of included surveys along with basic survey information.The compiled data contain over 8,000 clusters. On average, there are 25 surveyed

2A map of these countries can be found in Appendix B.1.3The one exception is the Mali 2001 survey. We must exclude this survey as it is not possible

to link the HIV results to individuals in the GIS-marked clusters.4As a robustness check, we also estimate using only the most recent survey from each country

and the results are unaffected.5Mozambique 2009 samples women up to age 64.6The age range for men is 15 to either 49, 54, 59 or 64, depending on the survey. See appendix

B.1 for details.7Testing success rates for each survey are shown by sex in Appendix table B.2. Refusal rates are

10%, on average. Mishra et al. (2006) examine test refusal rates in DHS testing, which are between1% to 22%, depending on the country. They conclude that although those refusing are more likelyto be positive, the DHS testing accurately represents national prevalence. In this study, individualsexposed to shocks do not differentially refuse a test (see Appendix Table B.3) so non-response doesnot induce bias in our results.

8For details regarding construction of the weights, see Appendix B.1.


individuals per cluster, and 90% of clusters contain between 10 and 50 surveyedindividuals. In total, there are over 200,000 individuals in the pooled data. Table3.1 also shows HIV prevalence rates for each survey. Overall, women’s prevalence is9.2% and men’s is 6.2%. However, these numbers mask a range that varies widelyfrom over 30% prevalence for women in Swaziland to less than 1% prevalence inSenegal. Given that the sexual behavior response to income shocks will have differentimplications depending on HIV prevalence, we classify countries into two groups: lowprevalence countries with less than 5%; and high prevalence countries with over 5%prevalence.9

Since the DHS surveys in each country were conducted in different years, weinclude survey fixed effects in all of our analysis. This controls for any effects thatnational policies might have on the HIV/AIDS epidemic as well as any time trendsof the epidemic. Our analysis is thus focused on making comparisons within countryin a given year.

Weather data and construction of shocks

To understand how economic shocks shape HIV outcomes, we seek a shock measurethat satisfies three criteria: derived shocks are economically meaningful, they areorthogonal to other factors that might also shape disease outcomes, and they capturethe potential disjoint between when HIV is acquired and when the individual isobserved in the DHS. Because we do not directly observe variation in economicperformance at a disaggregated level, and because such variation is likely endogenousto disease outcomes, we adopt an approach that is common in the literature anduse variation in weather as a proxy for variation in economic productivity. For thelargely agrarian societies of Africa, variation in weather directly shapes the economicproductivity of the majority of the population that continues to depend on agriculturefor their livelihoods (Davis et al., 2010). As we show below, particularly negativerainfall realizations substantially depress agricultural productivity across the region.

Our weather data are derived from the “UDel” (University of Delaware) data set,a 0.5 x 0.5 degree gridded monthly temperature and precipitation data set (Mat-suura and Willmott, 2009). These gridded data are based on interpolated weatherstation data and have global coverage over land areas from 1900-2008.10 Using the

9This categorization follows UNAIDS (2010). Appendix Figure B.2 shows that with the excep-tion of Cameroon, the prevalence classifications for each country remains stable for the ten yearspreceding the survey year. Our main results are unchanged when Cameroon is removed from ouranalysis.

100.5 degrees is roughly 50 kilometers at the equator. The UDel data are popular in economicapplications (recent papers include Jones and Olken (2010b); Dell, Jones, and Olken (2008)). Other


Table 3.1: DHS Survey Information

PrevalenceCountry Year Individuals Female Male Overall Category

1 Swaziland 2007 8,186 31.1% 19.7% 25.9% High2 Lesotho 2004 5,254 26.4% 18.9% 23.2% High3 Zambia 2007 26,098 21.1% 14.8% 18.1% High4 Zimbabwe 2006 10,874 16.1% 12.3% 14.2% High5 Malawi 2004 5,268 13.3% 10.2% 11.8% High6 Mozambique 2009 10,305 12.7% 9.0% 11.1% High7 Tanzania 2008 10,743 7.7% 6.3% 7.0% High8 Kenya 2003 6,188 8.7% 4.6% 6.7% High9 Kenya 2009 6,906 8.0% 4.6% 6.4% High10 Tanzania 2004 15,044 6.6% 4.6% 5.7% High11 Cameroon 2004 10,195 6.6% 3.9% 5.3% High

12 Rwanda 2005 10,391 3.6% 2.2% 3.0% Low13 Ghana 2003 9,554 2.7% 1.6% 2.2% Low14 Burkina Faso 2003 7,530 1.8% 1.9% 1.9% Low15 Liberia 2007 11,688 1.9% 1.2% 1.6% Low16 Guinea 2005 6,767 1.9% 1.1% 1.5% Low17 Sierra Leone 2008 6,475 1.7% 1.2% 1.5% Low18 Ethiopia 2005 11,049 1.9% 0.9% 1.4% Low19 Mali 2006 8,629 1.5% 1.1% 1.3% Low20 Congo DR 2007 8,936 1.6% 0.9% 1.3% Low21 Senegal 2005 7,716 0.9% 0.4% 0.7% Low

Total 203,796 9.2% 6.2% 7.8%

Prevalence estimates are weighted to be representative at the national level.

latitude/longitude data in the DHS, we match each DHS cluster to the weather gridcell in which it falls. Because lat/lon data in the DHS are recorded at the clusterlevel, all individuals within a given cluster are assigned the same weather. Our DHSdata match to 1701 distinct grid cells in the UDel data. To capture the seasonalityof agriculture, we construct grid-level estimates of “crop year” rainfall, where thecrop year is defined as the twelve months following planting for the main growing

rainfall data sets are available, but none were sufficient for our needs, lacking either sufficienttemporal coverage or spatial resolution.


season in a region.11 Annual crop year rainfall estimates are generated by summingmonthly rainfall across these twelve “crop year” months at a given location.

To capture shocks to economic productivity that are both meaningful and orthog-onal to potential confounders, one must identify years in which accumulated rainfallwas unusually low relative to what is normally experienced in a particular location.The most common way this has been done is by using the deviation from the localmean in a year or season, either in levels (as in Paxson, 1992; Fafchamps, Udry, andCzukas, 1998; Rose, 1999; Jayachandran, 2006; Tiwari, Jacoby, and Skoufias, 2013),in percentage (as in Dercon, 2004), or in standard deviation units (as in Hidalgoet al., 2010a). Unfortunately none of these methods is useful for summing shocksover a number of years, as the high years would offset the low years.12 To avoidthis offsetting, we require a binary rather than continuous indicator for whether ayear constitutes a shock or not. We define shocks as rainfall below a threshold thatis determined by the local rainfall distribution. In particular, for each of our 1701grid cells, we fit the history of crop-year rainfall realizations to a grid-specific gammadistribution and assign each grid-year to its corresponding percentile in that distribu-tion.13 A “shock” is then defined as a realization below a pre-determined percentilein the location-specific distribution. The literature does not provide definitive esti-mates of the percentile below which a shock becomes meaningful, and unfortunatelydisaggregated (e.g. grid) measures of economic productivity over time are unavail-able.14 To make progress, we construct an analogous measure of rainfall shocks atthe country level and assess how country-level agricultural productivity and GDP

11Estimates of planting dates are derived from gridded maps in Sacks et al. (2010); plantingof staple cereal crops for the primary growing season typically occurs in the boreal (northernhemisphere) spring across most of West and Central Africa, and in the boreal autumn across mostof Southern Africa.

12Other previously used continuous methods, which are also not useful for us, include the totallevel (or log of the level) in a season or year (as in Bruckner, 2012; Cole, Healy, and Werker, 2012),the timing of the onset of Monsoon or rainy season, days of rain in rainy season, and length oflongest dry spell in rainy season (as in Jacoby and Skoufias, 1998; Macours, Premand, and Vakis,2012). Also, Miguel, Satyanath, and Sergenti (2004a) employ year-over-year rainfall growth, which,as pointed out by Ciccone (2011a), is potentially a poor measure of shocks due to mean reversion.

13The gamma distribution was selected for its considerable flexibility in both shape and scale.Our results do not depend on the choice of gamma, or the estimation of the distribution moregenerally. Similar findings result from defining shocks as 1.5 standard deviations below the gridmean. We use the history of rainfall over the period 1970-2008, which was chosen to be a longenough period to be relatively insensitive to the recent shocks of interest, but short enough tocapture relatively recent averages if long run means are changing (e.g. with climate change).

14Others in the literature have constructed binary shocks using thresholds such as 75% or lessof the local mean (as in Shah and Steinberg, 2013) or 1 to 2 standard deviations below the localmean (as in Bobonis, 2009; Skoufias, Katayama, and Essama-Nssah, 2012).


growth respond to these shocks.15 Resulting estimates from panel regressions ofcountry level maize yields or GDP growth on percentile rainfall realizations (purgedof country- and time-fixed effects) are shown in Figure 3.1. Maize is the continent’sprimary staple crop, the crop grown by the majority of smallholder farmers, andthus perhaps the best direct measure of rural incomes. Point estimates from thesepanel regressions suggest that realizations below about the 15th percentile are themost harmful to maize yields (Figure 3.1, left panel). A similar pattern is found inGDP growth (right panel). We thus adopt this 15% threshold as our initial measureof a “shock” - i.e. we define a shock as a crop-year rainfall realization below the15% quantile of the local rainfall distribution - and show that our results are robustto other threshold choices in the neighborhood of 15%, as well as to other plausiblemethods of constructing binary shocks.

Finally, because the DHS only observes the disease status of a particular indi-vidual at one point in time, and an HIV+ individual could have become infectedat any time over the previous decade or longer (median survival time at infectionwith HIV in sub-Saharan Africa, if untreated, is 9.8 years (Morgan et al., 2002)),our main independent variable is the number of these shocks that have occurredover the 10 years prior to the survey year at a given location. For instance, if anindividual was surveyed in the DHS in 2007, the shock variable takes on a value ofbetween 0 and 10 corresponding to the number of crop-year rainfall realizations inthat individual’s region between 1997-2006 that fell below the 15% cutoff in the localrainfall distribution. We sum the shocks because acquiring HIV is irreversible – ifa shock led to an HIV infection 7 years ago, and that individual is still alive, theywill be HIV-positive today – and thus past shocks should have a demonstrable effecton current HIV infection. We again note that using a more continuous measure ofrainfall - e.g. deviations from average rainfall in levels - would tend to obscure pastshocks: the sum of a very bad year and a very good year would be similar to thesum of two normal years. The mean and standard deviation of shocks by cluster areshown in Table 3.2.

By construction, this shock measure should be orthogonal to other confoundingvariables. Because shocks at a given location are defined relative to that location’shistorical rainfall distribution, and the same percentile cutoff is used in each locationto define a shock (instead of the same absolute cutoff), all locations have the sameexpected number of shocks over any given 10 year period: each year any location

15That is, we aggregate crop year rainfall over all cells in a given country (weighting by crop area)to get a time-series of rainfall realizations for each country; we fit a separate gamma distributionto each country’s time series; and within each country each year is assigned it’s correspondingpercentile in its gamma distribution. Crop yield data are from FAO (2011), and data on real percapita economic growth is from the Penn World Tables 7.0 (Heston, Summers, and Aten, 2011).


Table 3.2: Shock Prevalence by Country

Prevalence Survey Mean SD Number of WeatherRank Country Year Shocks Shocks Clusters Grids

1 Swaziland 2007 2.90 0.46 275 132 Lesotho 2004 1.89 0.44 405 183 Zambia 2007 0.84 0.75 319 1464 Zimbabwe 2006 1.28 0.76 398 1225 Malawi 2004 1.04 0.75 521 536 Mozambique 2009 2.54 1.51 270 1157 Tanzania 2008 0.77 0.82 345 1678 Kenya 2003 1.17 0.62 400 819 Kenya 2009 1.22 0.78 398 9310 Tanzania 2004 1.92 0.93 475 17811 Cameroon 2004 1.59 1.06 466 112

12 Rwanda 2005 2.37 0.61 462 1413 Ghana 2003 1.31 0.80 412 7114 Burkina Faso 2003 1.28 0.90 400 8815 Liberia 2007 1.35 1.05 298 3716 Guinea 2005 1.34 0.75 295 7217 Sierra Leone 2008 3.00 0.00 353 2718 Ethiopia 2005 1.12 1.12 535 16719 Mali 2006 1.00 0.71 407 14920 Congo DR 2007 1.89 1.06 300 16821 Senegal 2005 0.70 0.69 376 61

Total 1.51 1.04 8110 1701


Figure 3.1: Effect of rainfall shocks on African maize yields (left panel) andper capita GDP growth (right panel)

-.15

-.1-.0

50

.05

.1lo

g m

aize

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ld

0 2 4 6 8 10rainfall decile

-2-1

01

23

Per c

ap G

DP g

row

th (%

)

0 2 4 6 8 10rainfall decile

Data are at the country level over the period 1970-2008, and include all sub-Saharan

African countries. Dark lines display point estimates from kernel-weighted local polynomial

regressions of the outcome on rainfall percentiles, after removing country and year fixed

effects. Grey areas represent 95% confidence intervals. Data sources are given in the text.

has a 15% chance of experiencing a shock. But because rainfall in a given locationvaries over time, some 10-year time windows will accumulate more shocks than otherwindows, and it is this plausibly random variation that we exploit.16 We confirmin Appendix B.2 that accumulated rainfall shocks are orthogonal to the first threemoments of the rainfall distribution, providing additional confidence that our shockmeasure is uncorrelated with other time-invariant unobservables that might alsoaffect HIV outcomes.

This definition of shocks assumes that relative (rather than absolute) deviationsin rainfall are what matter for income and HIV outcomes. This construction isnecessary for identification – using an absolute threshold for a shock would meanthat areas with lower or more variable rainfall would expect more shocks, and theseareas could differ in other unobserved ways that matter for HIV – but it is alsoplausibly captures what is important in our setting. Farmers choose crops that areadapted to the conditions under which they are grown, with farmers in drought-prone

16In Appendix B.3 we discuss why mean reversion is not a concern for our shock measure.


regions in Africa sowing crops (such as millet and sorghum) that can withstand lowrainfall realizations, and farmers in areas with higher average rainfall sowing cropsthat are generally higher yielding but less tolerate of drought (e.g. maize). Theresults in Figure 3.1, which are constructed using this relative shock measure, confirmthat relative deviations matter for both agricultural outcomes and broader economicperformance.

Estimation

To explore the effects of negative income shocks on individual HIV rates, we estimatethe following:

HIVijk = α + β1Stj +X ′iδ + γrj + ωk + εijk (3.2)

where HIVijk is an indicator for whether individual i in cluster j tested HIV-positivein survey k. Stj is the number of rainfall shocks that cluster j has experienced in the tyears before the survey. The default indicator for Stj is the number of crop-years withrainfall at or below the 15% quantile in the last 10 years for a given cluster. Noteagain that by construction, no one cluster is any more shock prone than another, i.e.E(Stm) = E(Stn) ∀j = m,n. All clusters expect the same total number of shocksover the 38 years in our rainfall data, and our identifying variation comes from therandom timing of these shocks: some clusters happen to receive more of their shocksin the decade immediately before we observe them, and others receive fewer. Both tand the definition of S are varied over a range to test the robustness of results.

The vector Xi contains characteristics of individual i that are not affected byshocks, specifically, gender and age. rj indicates that cluster j is rural. The surveyfixed effect is ωk and εijk is a mean-zero error term.17 We estimate linear probabilitymodels, allowing for correlation of error terms across individuals in the same weathergrid. Survey specific sampling weights are used to make the results representative ofindividuals living in these 19 countries in Sub-Saharan Africa (see Appendix B.1).

17There are a host of reasons for including survey fixed-effects. Innumerable differences acrosscountries exist that we cannot observe, including social norms of sexual behavior, male circumcisionrates, access to health services, and the national response to the AIDS epidemic. Such unobservabledifferences may also apply to different time periods within the same country, thus motivating awithin-survey estimation.


3.4 Results

Main results

Table 3.3 shows estimations of Equation 3.2, employing various samples and inter-action terms. The overall effect of shocks on HIV rates using the full sample is0.3 percentage points (ppt) and is statistically significant at the 10% level (Col-umn 1). Our simple conceptual framework predicts differential effects depending onwhether an individual lives in an urban or rural area, and in line with this predic-tion we find that the effects are concentrated in rural areas. We cannot reject thaturban effects are zero (Column 2; Linear combination), and the difference betweenestimates for rural and urban areas is borderline significant at conventional levels(p− value = 0.104). Focusing our analysis on rural areas (Column 3), we find thatshocks have a meaningful effect: we estimate that each shock leads to a 0.3 pptincrease in HIV prevalence, an effect that is significant at the 5% level and thatcorresponds to a 7.3% increase in HIV rates given a mean of 4.1%.

The second prediction from our framework is that increases in risky behavior as aresult of an income shock would result in little change in HIV infection rates if existingHIV prevalence is very low. To capture differential effects by baseline prevalence, wefocus on the rural sample and include an interaction between shocks and an indicatorfor low-prevalence countries. In countries with low prevalence (less than 5%), shockshave an approximately zero effect on HIV (Column 4; Linear combination), and wereject equality across low and high prevalence countries with 95% confidence (Column4; Shocks x Low Prevalence). Column 5 presents the estimation for the rural samplein high prevalence countries only. In these areas, each shock increases HIV by 0.8ppt, an 11% increase based on overall prevalence of 7%.

Finally, column 6 disaggregates the impact by gender. We find that shocks in-crease the probability of infection by 0.9 ppt for women and 0.6 ppt for men, bothof which are statistically significant at the 5% level. Given that HIV prevalence is8.3% for women and 5.6% for men in high prevalence rural areas, these estimatesrepresent large effect sizes of 11% increases in HIV per shock for both women andmen. We cannot reject that the effect size is the same across genders (Column 6;Shock x Male).

The magnitude of these effects are meaningful. In our entire sample, the meannumber of shocks is 1.5, which, combined with our primary results, suggests thatdrought-induced income shocks lead to a 17% increase in HIV risk over a ten-yearperiod. We also can attempt to roughly estimate an income elasticity with respectto HIV risk.18 We estimate that each drought shock results in a 7% to 10% loss in

18In order to generate an actual income elasticity with respect to HIV infection risk, we would


annual income (see Appendix B), which leads to an 11% increase in HIV infectionrisk. This result is similar to results from Robinson & Yeh (2011b) which showthat a 3% loss in income leads to about an 8% increase in HIV risk.19 Both resultssuggest that better means of consumption smoothing can have implications for theHIV/AIDS epidemic.

Robustness of results

In this section, we examine whether our primary result – the large response of HIVto shocks in rural, high prevalence areas shown in Table 3.3, column 5 – is robustto various issues of specification, variable definition, sample selection, or omittedvariables.

SpecificationWe first examine whether our results are sensitive to the specification or sample

used. We sequentially remove individual level controls, remove population weights,and replace survey-year-fixed effects with country- and year-fixed effects and our re-sults remain stable (Table 3.4; Columns 1-3). We also vary the sample used, removinghyper-endemic countries such as Swaziland and Lesotho where HIV-prevalence ex-ceeds 20%, and our results remain stable (Column 4). Finally, within each DHScluster (i.e. village), we remove all visitors from the sample, defined as those whohave lived in the area for less than a year at the time of the survey. We do thisfor two reasons. First, we want to identify the effect of shocks on HIV for thosewho were actually living in the area at the time of the shock and removing visitorshelps us establish this. Second, it may be that rainfall shocks are inducing NGO andgovernment workers to migrate in drought afflicted areas, and if these types are morelikely to be HIV+, than this could potentially explain our results. Removal of thesevisitors from the sample does not change our results (Column 5). We also present anestimate that employs only the most recent survey from each country, excluding theKE 2003 and TZ 2004 surveys, which produces similar results (Column 6). Finally,we provide results only for individuals who were between the ages of 15 and 50 whenthe shocks occurred (Column 7). These individuals would likely have the greatestresponse in terms of sexual behavior, and we do find a result that is slightly increasedover our main specification.

need: 1) percent of income derived from agriculture for all individuals in our sample, 2) individuallevel crop yields, and 3) crop prices by DHS cluster. This data is required for each year of the pastten years for everyone in our sample. Unfortuantely this data is not available.

19It is important to note that the sample used by Robinson & Yeh (2011b) consists of female sexworkers in Western Kenya, while the sample in this paper is representative of the rural populationin 19 countries.

CHAPTER 3. CLIMATE, ECONOMIC SHOCKS, AND HIV IN AFRICA 58T

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Shock definitionWe also examine the sensitivity of our results to the definition of a shock. While

our primary specification defines a shock as a crop-year rainfall realization belowthe 15th percentile of local realizations, the choice of the 15th percentile is some-what arbitrary. We vary the cut-off for shock definition in increments of 1 percentbetween the 5th and 40th percentile. The estimated coefficients for each percentileare presented in Figure 3.2. Overall, the point estimate is relatively stable aroundour default 15th percentile shock measure, and as the definition of a shock becomesless (more) severe the point estimates generally decrease (increase). Shocks in theneighborhood between between the 10th percentile to 20th percentile generate simi-lar results, although they become less precisely estimated the further they are fromthe 15th percentile (see appendix Table B.6).20

For rainfall at or above the 40th percentile, point estimates suggest that there isno effect on HIV. This corresponds to the estimated relationships between rainfall andmaize yields, and rainfall and GDP growth, shown in Figure 3.1. Both maize yieldsand GDP growth are unaffected by rainfall realizations above the 40th percentile,and consistent with this we find that HIV becomes similarly unaffected by rainfallaround this threshold.

We also vary the period of time over which shocks are summed, for comparisonwith our default definition of shocks summed over the past ten years. We sum shocksin 5-year bins (e.g. number of shocks 1-5 years before the survey, number of shocks6-10 years before, etc.) and employ each of these binned variables as the regressorin our main specification. Figure 3.2 plots the point estimates of these regressors.As we show in Appendix B.5, this time profile of the effect of shocks on HIV is verymuch as we would expect, with point estimates for the effect of shocks peaking earlywithin the 10-year window. Intuitively, an earlier shock has more time to reverberatethrough the population and generate additional infections compared to a more recentshock, but effects are attenuated over time as the earliest infected die. Given theobserved infection rate and the observed timing of mortality following infection, weshow via simulation in Appendix B.5 that the effect of a shock will peak 6-10 yearslater.

To address concerns that shocks from the mid-1990’s onward (our main shocks ofinterest, given our HIV data are from 2003 to 2009) may be endogenous to how shocksare defined, we also employ a shock definition that is based on the 15th quantile of thehistorical distribution derived from rainfall data only up through 1995. The cluster-

20Shocks that approach the 20th percentile may not be severe enough to effect behavior, whileshocks that approach the 10th percentile may have stronger effects on behavior, but their relativerarity reduces the statistical power of hypothesis tests.


specific definition of shocks then does not depend on anything that happened after1995. We find that the results do not differ significantly using this alternate measure(Table 3.4; Column 8). Finally, as an alternative to the quantile-based definition,we also define shocks as rainfall that is 1.5 standard deviations or more below thehistorical mean for the area. The primary estimation employing this definition ofshock is shown in column 9 of Table 3.4, where the estimated coefficient is similar,though slightly larger, and remains statistically significant.

Sample selectionDroughts can also effect other types of behaviors that might explain our results. If

shocks induce permanent out-migration and the migrants are disproportionately HIVnegative, this could yield a spurious correlation between observed shocks and higherHIV prevalence among the remaining population. In order to test whether selectivemigration can account for our results we conduct a bounding exercise suggested byLee (2009). Using national rural and total population figures by country, we estimatethat rural areas lose approximately 2% of population per shock (see Appendix B.4for more details) and conservatively assume that each one of these individuals isHIV-negative.21 We replace these individuals in our sample and re-estimate ourmain results. This in effect stacks the deck against finding a result: communitiesthat experience shocks now have more HIV-negative individuals. We note howeverthat the assumptions we make about migration rates are strong, and therefore somecaution is warranted when interpreting the results.

Table 3.5 first reproduces our primary result based on the rural sample of high-prevalence countries: the probability of infection increases by 0.8 percentage pointsper shock. We then vary the assumed percentage who migrate when a shock oc-curs, starting with our estimate of 2% and increasing in increments of 1%. We findthat when accounting for estimated out-migration of 2% per shock, the estimatedcoefficient (0.7 ppt) is nearly identical to our original estimate, and still significant.

Note that if all of rural to urban migration were caused only by shocks, then amore accurate estimate would be that 4% of the population migrates when a shockoccurs (again, see Appendix B.4 for details). Thus, the assumption of 4% loss pershock is an extreme upper bound. When we replace a 4% population loss per shock,our effect remains positive (0.4 ppt) and significant at the 10% level. Though 4%is the upper bound, we nonetheless report estimations under the assumptions of 5%and 6% loss per shock to show that the estimate does not lose significance until weassume 6% loss per shock – three times our best estimation of 2% loss per shock.This suggests that sample selection due to permanent migration is unlikely to explain

21In Section 3.5 we find no evidence of differential migration rates (due to shocks) betweenclusters close and far from urban centers.


our results.Omitted variablesA final concern is that our results might be driven by omitted variables. For

example, some aspects of local weather might be correlated with other unobservables(wealth, education, etc) that also affect HIV rates. While this is unlikely to betrue for our measure of rainfall shocks – by construction all areas expect the sametotal number of shocks over time – we confirm that our estimates are robust tocontrolling for characteristics of the underlying distribution. In Table 3.4, PanelB, we sequentially control for the first three moments of the rainfall distribution(mean, variance, skew) in our main specification (Columns 10-12), and also includeall three moments (Column 13). Our estimate remains stable throughout thesevarious specifications.

We can further test for these potential confounders with a “placebo” test - wecheck whether shocks in the future can predict present HIV rates or other observablepresent characteristics. Given that the DHS surveys were conducted between 2003and 2009, and our weather data ends in crop-years 2007-2008, we are only able toexamine shocks up to four years in the future.22 We find no relationship betweenHIV rates and shocks 1 to 4 years in the future (Table 3.6; Columns 1-4).23 We alsofind no relationship between current wealth quintile and future shocks (Columns 5-7), nor any relationship between an individual’s years of education and future shocks(Columns 8-10).

Finally, during the 2000’s, there was increasing access to antiretrovirals (ARVs)for HIV-positive individuals, which may bias our results if access was in any waycorrelated with shocks. We show that during most of our study time frame, ARVaccess was relatively low (less than 30% for all but one country) and that thereis no evidence that suggests ARV access is correlated with our shock measure (seeAppendix B.6). Taken together these tests provide additional evidence that shocksare picking up meaningful variation in economic conditions prior to the survey year,

22The only 2003 survey which has individual HIV infections (Kenya), does not have data onwealth and education. Therefore correlations with these characteristics can only be estimatedusing data in years 2004+, so these can only be observed up to three years in the future.

23We note that the estimates for shocks one year into the future may have measurement error.Because each DHS survey takes many months to complete, and because our data on which monthsare in the “crop-year” typically do not vary sub-nationally, the timing of a particular survey ina particular cluster may mean that some months of that cluster’s “future” crop-year could occurin the past. In the vast majority of our specifications, these problems “around the edges” areminimized by summing shocks over a ten year period. However, when looking just at shocks in thefuture 1 year, the rainfall measure in certain clusters might not perfectly capture rainfall 1 yearahead, making this particular estimate somewhat noisier.


Tab

le3.

5:R

obust

nes

sto

sam

ple

sele

ctio

nfr

omp

erm

anen

tm

igra

tion

Rep

laci

ng

lost

pop

ula

tion

shar

epersh

ock

Obse

rved

2%3%

4%5%

6%(1

)(2

)(3

)(4

)(5

)(6

)N

um

.sh

ock

spas

t10

yrs

..0

08**

*.0

07**

.006

**.0

05*

.004

*.0

04(.

003)

(.00

3)(.

003)

(.00

3)(.

003)

(.00

2)

Obse

rvat

ions

7776

081

792

8419

186

523

8877

591

330

R2

.030

.022

.023

.023

.024

.024

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ral

sam

ple

from

hig

h-p

reva

len

ceco

untr

ies.

Col

um

nhea

der

sd

enot

eth

ep

opu

lati

onsh

are

add

edto

the

sam

ple

to

acc

ount

for

out-

mig

rati

on

,as

sum

ing

all

out-

mig

rants

are

HIV

neg

ativ

e.N

ote

that

2%is

the

mos

tac

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tees

tim

ate

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h4%

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eu

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d(s

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).A

llsp

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ons

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ud

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ts.

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show

nin

par

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ster

edat

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gri

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vel.


Tab

le3.

6:P

lace

bo

Tes

ts

Dep

end

ent

Vari

able

HIV

Wea

lth

qu

inti

leY

rsof

Ed

uca

tion

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

(9)

(10)

Nu

m.

shock

sin

futu

re1

yr

.006

.005

-.15

2(.

006)

(.11

0)(.

232)

Nu

m.

shock

sin

futu

re2

yrs

-.00

2.1

13-.

134

(.00

7)(.

095)

(.19

4)

Nu

m.

shock

sin

futu

re3

yrs

-.00

4.1

04-.

146

(.00

7)(.

096)

(.19

4)

Nu

m.s

hock

sin

futu

re4

yrs

-.00

6(.

006)

Ob

serv

atio

ns

495

2343

881

2605

912

434

4952

343

881

2605

949

489

4386

126

039

R2

.044

.040

.025

.010

.031

.033

.029

.119

.118

.102

Ru

ral

sam

ple

from

hig

h-p

reva

len

ceco

untr

ies.

Not

eth

atth

eon

lysu

rvey

in20

03(K

enya

)d

oes

not

conta

inin

form

atio

n

on

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an

ded

uca

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;th

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ore

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late

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inth

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ture

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ther

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ds

in20

07-2

008

crop

year

s.A

llsp

ecifi

cati

ons

incl

ude

contr

ols

for

gen

der

,

age

and

surv

eyfi

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ts.

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imat

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and that this variation is uncorrelated with other factors that might also explaindisease outcomes.

Figure 3.2: Effect of rainfall shocks on HIV, by severity (left panel) andtiming (right panel)

-.005

0.0

05.0

1.0

15.0

2im

pact

of s

hock

on

HIV

5 10 15 20 25 30 35 40percent shock

-.01

0.0

1.0

2co

effic

ient

on

shoc

k va

riabl

e

-30 -25 -20 -15 -10 -5 0Years before survey year

The black line represents the coefficient point estimates of the impact of a particular rainfall

shock on HIV for the rural sample from high-prevalence countries, using (A) various defi-

nitions of “shock” accumulated over the previous 10 years and (B) 15% shocks accumulated

over different time periods, including placebo future shocks up to 3 years past the survey

date. Plot A: dotted lines represent the 95% confidence intervals; dashed lines represent

the 90% confidence intervals. Plot B: shaded area represents 95% confidence interval.

3.5 Exploring Pathways

Behavioral pathways

How might changes in income induce behavioral changes that increase HIV infection?As HIV is overwhelmingly transmitted by heterosexual sex in this context, we firstexamine whether risky sexual behaviors increase in response to recent shocks, usingself-reported sexual behavior. We then consider three separate coping behaviors thatcould lead to increased sexual risk.


Risky sexual behavior

The use of self-reported sexual behavior is subject to a few caveats. There is alarge body of evidence that suggests self-reported sexual behavior suffers from socialdesirability bias (Cleland et al., 2004) and that women significantly under-reporttheir sexual activity (Minnis et al., 2009).24 In addition, we only have measures ofsexual behavior during the 12 months prior to the survey. It is not immediatelyclear which time window of shocks should be considered to impact sexual behaviorin the past 12 months. Certainly shocks in the current and previous year should,however, given the potential lag between lack of rainfall and lack of income, perhapsdroughts two years ago should have a similar impact. Further, more distant shocksthat induced the creation of new sexual relationships may have continuing impactson current behavior if those relationships (or behaviors) are persistent.25 For thisreason, we present the impact on recent sexual behavior of shocks within the past 10years, shocks within the past 5 years, and having a shock that affected income overthe past 12 months. Given these caveats, we interpret results on self-reported sexualbehavior with caution.

The outcome variables we examine are whether in the past 12 months the respon-dent has (i) been sexually active, (ii) had multiple partners, or (iii) had non-spousepartner(s).26 Table 3.7 shows results of estimations of Equation 3.2, separately bygender, with these self-reported sexual behaviors as the dependent variables regressedseparately on three categories of independent variables as noted. A strong and con-sistent finding is that both men and women are significantly more likely to haveengaged with a non-spouse partner if exposed to a shock in any of the three timeperiods considered. For both men and women, shocks affecting the past 12 monthsincrease non-spouse partnership rates by about 10-20%. Shocks in nearly all of theperiods also increase the likelihood of engaging with multiple concurrent partnersby 10-15%, though the estimates are not precise in all periods. Point estimates for

24Additional caveats are that data that is available for sexual behavior doesn’t capture all aspectsof risky behavior that could lead to HIV infection. For example, the type of sexual partner youhave (commercial sex worker, individual with multiple partners, etc.) will affect the likelihood ofHIV infection, but such data are not available in the DHS. In addition, the questions about sexualbehavior are not present in all the employed DHS surveys, and therefore the analysis is performedon a sub sample of our data.

25Swidler and Watkins (2007) cite multiple works documenting long-term extramarital unions inexchange for transfers. In addition, the sex-workers in Robinson and Yeh’s (2011b) study startedas sex-workers on average 9.7 years prior to the study.

26In this data, a monogamous cohabiting union is considered a spousal partner, irrespectiveof formal marital status. Also, single, sexually active individuals are included in those havingnon-spouse partners.


the impact of shocks on being sexually active at all are positive for men, but notsignificantly different from zero, and for women are not consistent across the periodsconsidered.

Overall, these self-reports of sexual behavior indicate that individuals who haveexperienced recent shocks are more likely to report risky sexual activity. Keepingthe caveats discussed earlier in mind, these findings suggest that shocks are indeedchanging sexual behavior – and in particular leading to riskier sexual behavior –and that these behavioral changes are what likely link rainfall shocks to HIV. Inthe remainder of this section, we seek evidence for which coping behaviors may beprimarily responsible for this relationship.

Temporary Migration

One response to drought-induced income shocks is to migrate from rural to urbanareas in search of employment (Skoufias, 2003; Ellis, 2000). Migration is associatedwith greater levels of risky sexual activity and higher rates of HIV (Lurie et al., 2003;Brockerhoff and Biddlecom, 1999). Individuals may temporarily migrate to urbanareas in response to droughts, acquire HIV due to additional partnerships or high-risk partners, and then infect others when returning to their rural communities.27 Ifincome shocks induce temporary migration, then ∂p

∂z< 0 for both men and women,

as both the migrant and his/her partner in the rural village would face increasedrisk.

As a check for this pathway, we use information on the number of times individualshave been away from home in the past 12 months, and whether any time away haslasted more than one month. If temporary migration is a primary coping behavior inthis setting, we would expect that a shock in the past year would significantly increaseboth indicators. These outcomes are available for men in 17 (and for women in 9) ofour 21 surveys, and estimation results are presented in Table 3.8. For comparison,the main estimation from Table 3.3, col. 5 is presented in cols. 1 and 2, for men andwomen respectively, for these sub-samples.

Cols. 3-6 of Table 3.8 show that for both men and women, shocks affectingthe past 12 months have a correlation with the number of times away from homeand being gone for more than one month in the past year that is either negative orindistinguishable from zero. We have disaggregated this effect for individuals who

27Note that, if the migration is of a permanent nature, this should not affect HIV in the ruralarea, though it may affect our estimation of rural HIV, due to sample selection. We directly addressthis in section 3.4.


live near to an urban area versus those in more remote areas.28 Neither of these sub-samples exhibit more frequent temporary migration when exposed to a shock.29 Thissuggests that in our rural sample, droughts are not inducing significant temporarymigration.

Dropping-out and Early marriage

A second set of coping behaviors that may affect sexual risk are changes in schoolingand marriage behavior. In SSA, a common response to a negative income shockis to withdraw children from school (Ferreira and Schady, 2009), which appearsparticularly true for girls (Bjorkman, 2013). Once a girl has withdrawn from schoolshe is much more likely to be sexually active and to marry (Osili and Long, 2008;Duflo, Dupas, and Kremer, 2011; Ozier, 2011), both of which are risk factors forHIV (Clark, 2004; Baird, McIntosh, and Ozler, 2011). Furthermore, households maymarry-off daughters earlier in response to a shock, especially in regions where bridepayment is customary (Hoogeveen, van der Klaauw, and van Lomwel, 2011; Jensenand Thornton, 2003). If income shocks induce early drop-out and early marriage,which result in earlier sexual activity, then ∂p

∂z< 0. While this could apply to both

men and women, young women would be most affected through this channel. Ifearly marriage is the pathway, either as a direct response to shocks or as a result ofwithdrawing from school, we would expect droughts to be associated with a youngerage at marriage, and increased probability of marriage at the time of the survey.Further, if shocks are inducing drop-out, we would expect shocks to be associatedwith fewer years of schooling and expect shocks to have the strongest effects on HIVfor women who were school-aged at the time of the shock.

The first two columns of Table 3.9 show estimates of the impact of shocks occur-ring when a woman was potentially subject to early marriage on whether she hasever married by the time of the survey.30 As mean age at marriage for women inthis sample is 18, women are considered at risk for early marriage when aged 13 to18 (col. 1) or aged 15 to 20 (col. 2). In neither case do shocks yield a significantincrease in the likelihood of marriage at or before the time of the survey.

The second two columns estimate the impact of shocks during the same periods oflife on the resulting age at marriage for those who have ever married. The coefficients

28Near to urban is defined as being within 100km of an urban center with population 250,000or more. Urban populations are from the Global Rural-Urban Mapping Project.

29These results look very similar when employing shocks during the past 2 or 3 years, ratherthan 12 months; results not shown.

30Only shocks occurring during the HIV epidemic are considered (1980 or later), as only thesecould be driving the results found.


reflect an effective zero change in age at marriage when exposed to a shock at thesecritical ages. In short, it seems that shocks do not induce earlier marriage for womenin this sample.

Even if youth are not marrying earlier, households may respond to income shocksby withdrawing children from school, especially girls. Girls that drop out early areat higher risk for early sexual activity and HIV transmission (Baird et al., 2010). Ifthis is a contributing factor in the link between rainfall and HIV, we would expectto find two telltale results. First, shocks should reduce total schooling for womenwho were school-aged when the shock occurred; second, the link between rainfalland HIV should be restricted to women who had not yet completed their schoolingwhen the shock occurred. Columns 5 and 6 of Table 3.9 estimate the effect of shockswhen aged 13 to 18 (and 15 to 20) on years of education. Both estimates producea negative coefficient, however, both reflect effect sizes of less than 1% and are notstatistically different from zero. We do not find evidence that rainfall shocks inducesignificant dropping out of girls.31 Finally, columns 7 and 8 replicate our primaryestimation, excluding women who were school aged during the past 10 years. Wefind that the results are robust to this exclusion, suggesting that women who wereschool-aged at the time of the shock are not driving the results. In sum, we findno evidence that early marriage and dropping out are the primary coping behaviorlinking rainfall to HIV.

Transactional Sex

A third coping mechanism is engaging in transactional sex. Transactional sex isthought to be common in sub-Saharan Africa, and is broadly defined to includeboth prostitution as well as transfers within casual relationships and long-term part-nerships (Luke, 2006; Swidler and Watkins, 2007; Bene and Merten, 2008; Hunter,2002; Maganja et al., 2007; Leclerc-Madlala, 2002).32 Women may respond to incomeshocks either by taking on additional partnerships or engaging in more frequent orriskier sexual activity (i.e. unprotected sex) to increase transfers. Both types of be-haviors have been documented throughout sub-Saharan Africa, with women in ruralMalawi engaging in multiple partnerships in response to income insecurity (Swidler

31These findings are consistent with work by Shah and Steinberg (2013), showing that childrenin India actually attend school less when rains are plentiful as there is more work to be done outsideschool.

32One could argue that early marriage as a response to an income shock may also be consideredtransactional sex in some form. We argue that these are conceptually distinct as early marriagewould be an increase in sexual activity at the extensive, rather than the intensive margin. Further,these are distinct from a policy perspective.


and Watkins, 2007), and women in South Africa and Western Kenya more likelyto engage in unprotected sex as a response to negative income shocks (Dinkelman,Lam, and Leibbrandt, 2008; Robinson and Yeh, 2011b; Dupas and Robinson, 2012).While there are many factors affecting the HIV/AIDS epidemic, transactional sex isthought to be a major driver within SSA (Alary and Lowndes, 2004; Dunkle et al.,2004; Cote et al., 2004), and a growing empirical literature suggests that economicconditions affect risky sexual behavior and the market for transactional sex (Bairdet al., 2010; Kohler and Thornton, 2012; Robinson and Yeh, 2011a).

We cannot directly examine changes in this behavior, as we lack data on trans-actions.33 To make progress, we make a few assumptions on the transactional sexmarket. First, we follow the literature in assuming that women supply and men de-mand transactional sex (Edlund and Korn, 2002). Second, in keeping with a recentmicro literature (Baird et al., 2012; Kohler and Thornton, 2012; Robinson and Yeh,2011b), we assume that women increase their supply of transactional sex if othersources of income decrease; and that when supply increases, prices fall. Finally, weassume that individuals experiencing larger income shocks should have a strongerbehavioral response – that is, supply is increasing and demand is decreasing in shockexposure.

While we do not observe individual changes in income, we do observe occupation– in particular, whether or not an individual’s primary income source is from agri-culture.34 We assume that incomes of individuals working in agriculture are moresensitive to drought than those working outside agriculture. In the market for trans-actional sex, we would expect that men working outside agriculture would increasetheir quantity demanded in the face of an aggregate shock, based on the reducedprice. Further, men working in agriculture would reduce their quantity demanded.However, as men working in agriculture will also face increased network risk, the ef-

33Whether a man has paid for sex in the past year is only queried in four surveys from highprevalence countries. This likely only captures explicit prostitution, rather than all forms of trans-actional sex, as the reporting is low (3%). Women are not queried regarding payment for sex in anyof our surveys. In addition, examining whether women are entering the transactional sex market, orare simply make changes on the intensive margin as a response to shock would be very interesting,however, given these data limitations, we are unable to say anything about this topic.

34We are able to classify individuals by their employment type at the time of the survey butnot at the time of the shock. Our analysis thus makes the assumption that occupation is fairlypersistent: individuals in agriculture at the time of survey are more likely to have been in agricultureat the time of the shock, and thus our occupational categories are meaningful. We include onlythose employed in the last year, as the unemployed do not report an occupation. As such, it isdifficult to assume whether the currently unemployed previously worked in agriculture or not. Aconcern with using occupational category is that it may be endogenous to shocks. We examine thepredictive effect of number of shocks in the past 10 years on current employment in rural areas, tocheck its potential to induce bias. Shocks have no predictive effect for employment in agriculture.


fect of shocks on their HIV status should be dampened but not necessarily reversed,relative to men working outside agriculture. Before turning to the results, we stressthat given the assumptions we make, our findings in this section warrant caution.While our results are consistent with transactional sex being the channel linkingshocks to HIV, we cannot definitively claim this. Future research with comprehen-sive data on shocks, sexual behavior, and transfers will shed more light onto thischannel.

Table 3.10 presents the primary estimation for both men and women, with in-teractions by occupation. For women, the effects of shocks appear concentrated onagricultural women (Column 4; Row 1), while women in the non-agricultural sectorappear relatively unaffected by shocks (Column 4; Row 5).35 These results makessense as income of agricultural women is most affected by a drought; these results arealso consistent with various channels. To sharpen our analysis, we examine the effectsof shocks on men separated by occupation. We find the impact on non-agriculturalmen’s HIV risk is large and significant at the 10% level (Column 2; Row 5), while theeffects of shocks for agricultural men is nearly zero (Column 2; Row 1). While wecannot reject the null that shocks have the same effect for men in and outside of agri-culture (p-value = .167), these estimates are consistent with transactional sex beingthe channel linking shocks to greater HIV rates.36 If shocks are inducing women tosupply more sex, then men whose incomes are least affected by droughts (i.e. menemployed outside of agriculture) should increase their demand. While men in agri-culture would face lower prices in the market for transactional sex, their income willalso be affected by drought, dampening any price effects.

Finally we note that our shock measure is an aggregate level shock that wouldpresumably effect the incomes of all men and women in an area (regardless of oc-cupation). However, it maybe the case that men are better insured against shocksthan women (see Dercon and Krishnan, 2000) which may lead women to be moreresponsive to aggregate shocks than men. Our findings are consistent with this viewas well as previous work that finds the supply side responding more to aggregateshocks than the demand side (Dupas and Robinson, 2012; Wilson, 2011).

To then summarize the results from this section, our main finding is that indi-

35We cannot reject the null that shocks have the same effect on women in and outside of agri-culture (p-value = .252).

36We also find that the magnitude of increases in HIV are consistent with increases in trans-actional sex. Robinson and Yeh (2011a) find that an individual level health shock that results intotal income loss for one day leads a woman to increase her number of sexual partners the followingday by 0.3, an 18% increase in their sample. We find that this is comparable to our findings thata year-long income shock increases a woman’s lifetime partnerships by about 33%. See simulationin appendix B.7.


viduals exposed to recent drought events are more likely to be infected with HIV(∂HIV∂S

> 0). Given the strong evidence of both the relationship between droughts

and income(∂z∂S> 0)

and risky sexual behavior and HIV(∂HIV∂p

> 0)

, this suggests

that the underlying mechanism connecting droughts and HIV is a behavioral re-sponse to income shocks that is leading to increased sexual risk

(∂p∂z< 0). We find

no evidence that temporary migration or dropping out /early marriage are the keydrivers of this relationship. This section provides evidence that is broadly consistentwith transactional sex as a pathway. However, we cannot conclusively establish theprimary behavior driving this result, nor can we rule out any single behavior as acontributing factor.

Non-behavioral pathways

Each type of behavior discussed above - early sexual activity, migration, transac-tional sex - has a well-documented connection to HIV risk and a plausible link tocommunity-level income shocks. However, droughts also have documented effects onother important factors in rural areas, such as nutrition and civil conflict. We arguethat the evidence linking these factors to HIV outcomes is, at best, inconclusive, andthat they are unlikely to be pathways that link shocks to HIV.

For HIV infected individuals, malnutrition is associated with higher mortalityrates and higher viral loads (John et al., 1997; Weiser et al., 2009). Thus the effectthat malnourished HIV-positive individuals will have on the epidemic is ambiguous;higher mortality rates would lead to fewer HIV-positive individuals but higher viralloads would make them more infectious.37 For HIV-negative individuals, little isknown about the relationship between malnutrition and susceptibility to HIV infec-tion (Mock et al., 2004). Though malnutrition may lead to a compromised immunesystem which could play a role in susceptibility (Schaible and Stefan, 2007), to thebest of our knowledge there is no work that demonstrates an increase susceptibilityto HIV infection for malnourished HIV-negative individuals. While we cannot ruleout that this is a contributing pathway, given the existing evidence it does not appearto play a primary role in the HIV/AIDS epidemic.

Some recent evidence suggests that negative rainfall deviations are associatedwith higher incidence of civil conflict in Africa (Miguel, Satyanath, and Sergenti,2004a; Hsiang, Burke, and Miguel, 2013). This could indicate another pathway be-tween rainfall and HIV if civil conflict has a direct effect on disease outcomes, forinstance due to conflict-related sexual violence. While we again cannot directly rule

37We note, however, that high viral loads may make individuals too sick to be sexually active(see Thirumurthy et al., 2012).


able

3.7:

Explo

ring

Beh

avio

rs:

Incr

easi

ng

risk

yse

xual

beh

avio

r

Wom

enM

enSex

ual

lyM

ult

iple

Non

spou

seSex

ual

lyM

ult

iple

Non

spou

seA

ctiv

eP

artn

ers

Par

tner

Act

ive

Par

tner

sP

artn

er(1

)(2

)(3

)(4

)(5

)(6

)N

um

.sh

ock

spas

t10

yrs

..0

12**

.003

*.0

07*

.008

.018

***

.015

**(.

005)

(.00

2)(.

004)

(.00

6)(.

004)

(.00

6)

Obse

rvat

ions

4314

543

119

4314

734

607

3456

334

613

R2

.060

.011

.018

.223

.034

.051

Num

shock

spas

t5

yrs

.021

***

.004

*.0

13**

.008

.016

**.0

21**

(.00

7)(.

002)

(.00

5)(.

009)

(.00

6)(.

009)

Obse

rvat

ions

4314

543

119

4314

734

607

3456

334

613

R2

.060

.011

.018

.223

.033

.050

Y/N

shock

affec

ting

pas

t12

mo

-.02

7**

.003

.023

**.0

13-.

007

.035

**(.

012)

(.00

4)(.

010)

(.01

2)(.

012)

(.01

7)

Obse

rvat

ions

4314

543

119

4314

734

607

3456

334

613

R2

.059

.011

.018

.222

.032

.051

Mea

nof

Dep

Var

..7

59.0

24.1

20.7

38.1

54.2

69R

ura

lsa

mp

lefr

om

hig

h-p

reva

len

ceco

untr

ies.

Dep

end

ent

vari

able

sar

ese

xu

alb

ehav

iors

inth

ep

ast

year

.“N

on-s

pou

se”

ind

icat

esse

xw

ith

an

on

-sp

ou

sep

artn

er;

this

incl

ud

esal

lse

xfo

rsi

ngl

ein

div

idu

als.

All

spec

ifica

tion

sin

clu

de

contr

ols

for

age

an

dsu

rvey

fixed

effec

ts.

Est

imat

ion

sar

ew

eigh

ted

tob

ere

pre

senta

tive

ofth

e19

cou

ntr

ies.

Rob

ust

stan

dar

d

erro

rsare

show

nin

par

enth

eses

clu

ster

edat

the

grid

level

.


Tab

le3.

8:E

xplo

ring

Beh

avio

rs:

Tem

por

ary

mig

rati

on

Mai

nH

IVre

sult

Aw

ayfo

rm

onth

+T

otal

tim

esaw

ayfo

rth

issu

b-s

ample

inpas

tye

arin

pas

tyr

Men

Wm

nM

enW

mn

Men

Wm

n(1

)(2

)(3

)(4

)(5

)(6

)N

um

.sh

ock

spas

t10

yrs

..0

07*

.015

***

(.00

3)(.

004)

Y/N

shock

inpas

tyr

-.01

0.0

18-.

421*

**-.

229*

*(.

024)

(.01

8)(.

149)

(.11

5)

Nea

rurb

an*

shock

inpas

tyr

-.01

8-.

008

-.41

9-.

569*

**(.

031)

(.02

7)(.

282)

(.18

8)

Nea

rurb

an-.

008

-.00

9-.

148

.162

*(.

011)

(.01

2)(.

199)

(.08

4)O

bse

rvat

ions

2609

626

299

2613

326

300

2380

222

990

R2

.038

.041

.004

.016

.025

.117

Mea

nof

Dep

Var

.064

.094

.151

.130

2.06

4.9

90

Ru

ral

sam

ple

from

hig

h-p

reva

len

ceco

untr

ies.

Th

e“N

ear

urb

an”

vari

able

ind

icat

esw

het

her

agi

ven

clu

ster

isw

ith

in

100k

mof

anu

rban

area

(defi

ned

asp

opu

lati

onsi

ze25

0K+

);th

isre

pre

sents

27%

ofth

eru

ral

pop

ula

tion

inh

igh

pre

vale

nce

cou

ntr

ies.

Urb

an

pop

ula

tion

sar

efr

omth

eG

lob

alR

ura

l-U

rban

Map

pin

gP

roje

ct.

Var

iab

les

onb

ein

gaw

ay

are

not

avai

lab

lefo

rall

cou

ntr

ies

(see

text)

;th

em

ain

esti

mat

ion

for

thes

esu

b-s

amp

les

are

give

nin

Col

s.1

and

2.A

ll

spec

ifica

tion

sin

clu

de

contr

ols

for

age

and

surv

eyfi

xed

effec

ts.

Est

imat

ion

sar

ew

eigh

ted

tob

ere

pre

senta

tive

ofth

e19

cou

ntr

ies.

Rob

ust

stan

dard

erro

rsar

esh

own

inp

aren

thes

escl

ust

ered

atth

egr

idle

vel

.


Tab

le3.

9:E

xplo

ring

Beh

avio

rs:

Ear

lysc

hool

dro

p-o

ut

and

mar

riag

e

Dep

enden

tV

aria

ble

:E

ver

mar

ried

Age

atm

arri

age

Yea

rsof

Educ

HIV

Sta

tus

Age

d25

+A

ged

30+

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Num

.sh

ock

s,ag

ed13

to18

-.00

0.0

00-.

010

(.00

5)(.

046)

(.05

6)

Num

.sh

ock

s,ag

ed15

to20

-.00

3.0

06-.

005

(.00

5)(.

057)

(.05

4)

Num

.sh

ock

spas

t10

yrs

..0

11*

.016

**(.

006)

(.00

6)O

bse

rvat

ions

2467

922

679

2377

023

005

2742

925

242

1228

038

45R

2.1

25.0

65.0

33.0

23.2

23.2

22.0

31.0

22M

ean

Dep

Var

.881

.923

18.1

18.3

5.5

5.4

.091

.067

Fem

ale

,ru

ralsa

mp

lefr

om

hig

h-p

reva

len

ceco

untr

ies.

Th

efi

rst

six

colu

mn

sex

amin

eth

eim

pac

tsof

shock

sth

atocc

urr

ed

wh

enw

oman

was

inth

en

ote

dage

ran

ge,

sin

ceth

est

art

ofth

eep

idem

ic(1

980)

.T

he

last

two

colu

mn

sex

amin

eth

e

imp

act

ofsh

ock

sin

the

pas

t10

year

son

HIV

for

wom

enw

ho

wer

eab

ove

am

inim

um

age

du

rin

gal

lof

the

pas

t10

year

s.A

llsp

ecifi

cati

ons

incl

ude

contr

ols

for

age

and

surv

eyfixed

effec

ts.

Est

imat

ion

sar

ew

eigh

ted

tob

ere

pre

senta

tive

of

the

19

cou

ntr

ies.

Rob

ust

stan

dar

der

rors

are

show

nin

par

enth

eses

clu

ster

edat

the

grid

level

.


out this possibility in our data, recent studies find no clear link between conflict andHIV in either the observational data from Africa (Spiegel et al., 2007), or using epi-demiological models that attempt to explain observed HIV prevalence with reportedrates of sexual violence (Anema et al., 2008). We have thus focused our empiricalexploration of pathways on the the three coping behaviors described above.

3.6 Macro level implications

Our results suggest that community-level economic conditions play an important rolein an individual’s risk of HIV infection. A natural question is the extent to whichour results inform broader observed patterns of HIV prevalence on the continent. Inother words, can income shocks help explain the striking country-level variation inHIV prevalence across sub-Saharan Africa? Given that our estimation strategy aboveuses only within-country variation, and that we only have individual-level HIV datafor about half of the countries in the Sub-Saharan region spread out over differentyears, it’s not obvious that our estimates should inform these broader patterns.

To address this question, we apply our basic approach to country-level estimatesof HIV prevalence provided by UNAIDS. UNAIDS estimates of country level HIVprevalence over time build heavily on HIV surveillance data distinct from what is inthe DHS (e.g. data from antenatal testing at designated clinics), and thus provideprevalence estimates that are somewhat independent from the DHS biomarker datawe focus on above. We use the same gridded climate data to derive a time series ofannual average rainfall for each country, where the observation for a given country-year is a weighted average of all the grid cells in that country, using percent of eachcell covered by cropland as weights.38 Similar to above, we calculate these annualrainfall totals for each country back to 1970, fit a separate gamma distribution toeach country’s time series, and define a shock as a year in which country-averagerainfall fell below the 15th percentile in that country’s rainfall distribution. We thenseek to explain the cross-sectional prevalence in HIV in a given year as a function ofaccumulated shocks over the previous decade. This regression uses a different sourceof variation from our individual specifications (cross-country rather than within-country), uses data that are related but distinct, and includes many countries not inour individual-level data. It thus provides a test of the relationship between shocksand HIV that is substantially distinct from the results presented above.

38This provides country-level rainfall estimates that are relevant for agriculture but that are alsoeffectively weighted by rural population density, since areas that are farmed more intensively inrural Africa tend to be areas with higher population density (given very small average farm plotsize).


Tab

le3.

10:

Explo

ring

Beh

avio

rs:

Impac

ton

HIV

by

exp

osure

todro

ugh

t-in

duce

din

com

esh

ock

Men

Wom

en(1

)(2

)(3

)(4

)(1

)N

um

.sh

ock

spas

t10

yrs

..0

04.0

02.0

09**

.011

***

(.00

3)(.

003)

(.00

4)(.

004)

(2)

Non

-Ag

*Shock

s.0

07-.

007

(.00

5)(.

006)

(3)

Non

-Ag

emplo

ym

ent

.049

***

.116

***

(.01

6)(.

023)

(4)p−value

onin

tera

ctio

n.1

67.2

52

(5)

Impac

tof

shock

son

Non

Ag

(lin

.co

mb.)

.009

*.0

04(.

004)

(.00

6)O

bse

rvat

ions

3758

537

585

3748

737

487

R2

.033

.039

.032

.039

Mea

nD

epV

ar(A

g).0

56.0

77M

ean

Dep

Var

(Non

-Ag)

.096

.148

Sam

ple

from

hig

h-p

reva

len

ceco

untr

ies.

All

spec

ifica

tion

sin

clu

de

contr

ols

for

age

and

urb

an,

and

surv

eyx

emp

loym

ent

typ

efi

xed

effec

tsto

allo

wth

eco

rrel

atio

nb

etw

een

HIV

and

occ

up

atio

nto

vary

by

cou

ntr

y.N

ote

that

Non

Ag

ind

icat

or

alo

ne

isin

dic

ativ

eon

lyfo

rth

eco

untr

yex

clu

ded

infi

xed

effec

ts(M

ozam

biq

ue)

.E

stim

atio

ns

are

wei

ghte

dto

be

rep

rese

nta

tive

ofth

e19

cou

ntr

ies.

Rob

ust

stan

dar

der

rors

are

show

nin

par

enth

eses

clu

ster

edat

the

grid

leve

l.


Figure 3.3: Country-level HIV prevalence & Shocks

ANG

BEN

BOT

BFA

BURCAM

CAR

CHACON

CDI

ERI

GAB

GAM

GHAGUIGMB

KEN

LES

LIB

MAD

MWI

MLI MAU

MOZ

NAM

NIG

NGARWA

SENSLE

SAF

SWZ

TAN

TGO

UGA

ZAM

ZIM

05

1015

2025

HIV

prev

alen

ce

0 1 2 3 4shocks

ANGBEN

BOT

BFABUR

CAM

CARCHA CONCDI

ERI

GAB

GAMGHA GUIGMB

KEN

LES

LIBMAD

MWI

MLIMAU

MOZNAM

NIG

NGARWA

SENSLE

SAF

SWZ

TANTGO

UGA

ZAM

ZIM

05

1015

2025

HIV

prev

alen

ce

0 1 2 3 4 5shocks

The left panel presents results for HIV prevalence in 1999 (y-axis) and accumulated shocks

over the previous decade (x-axis). The right panel presents results for HIV prevalence in

2008 and accumulated shocks since 2000. HIV data are from UNAIDS (2010). Dark lines

are linear least squares fits, with gray areas representing the 95% confidence interval. Data

are jittered to make country labels more legible.

Figure 3.3 plots these relationships for the two decades for which UNAIDS re-ports data. Countries with a higher number of shocks are more likely to have higherlevels of HIV-prevalence; this is true both in the 1990s (left plot) when the epi-demic was growing rapidly, as well as in the 2000s, when the epidemic has plateauedor started to decline in many countries. These simple cross sectional relationshipsare statistically significant and explain 14-21% of the cross-sectional variation in HIVprevalence across the continent (see Appendix B.8 for regression results).39 Again, aswith our individual-level results this estimate is not picking up differences in under-lying propensity to experience shocks (which could be correlated with other factorsaffecting HIV), but relies instead on the random timing of recent shock exposure.

We draw three implications from these results. First, the fact that we can repli-

39We also explore whether shocks can explain the time-path of the epidemic by looking at cross-country decadal changes in HIV prevalence as a function of accumulated shocks. Effect sizes areagain large but not always quite significant at conventional levels (p=0.12 on the shock variable for1990s changes), and we explain somewhat less of the cross-country variance in decadal trends thanwe do in levels. Nevertheless, results are broadly consistent with cross-sectional results.


cate our basic micro level results using different sources of variation on both the left-and right-hand side gives us additional confidence that economic conditions exertsignificant influence on HIV outcomes. Second, our results suggest that bad luckwith the weather might have played a surprising role in shaping observed patterns ofthe AIDS epidemic across the African continent: countries that were hit with largenegative shocks during the early years of the epidemic have much higher infectionrates many years later. Finally, and somewhat more speculatively, given that manyareas in sub Saharan Africa lack social safety nets and depend heavily on rainfed agri-culture, recurring droughts may play an important and prominent role in explainingwhy the AIDS epidemic has disproportionately affected sub-Saharan Africa.

3.7 Conclusion

Ultimately any halt to the AIDS epidemic will require a medical intervention, such asa vaccine or methods approximating one (e.g. the aggressive use of ARVs). However,our results suggest that economic factors, and in particular the ways in which indi-viduals respond to changes in their economic environment, also play an importantrole in shaping outcomes in the epidemic. As such, our findings unite two widely-held notions among researchers in the HIV/AIDS community: that heterosexual sexis a primary driver of the AIDS epidemic in sub-Saharan Africa, and that economicconditions play some role in sexual behavior in these countries.

Our paper provides compelling evidence that a deterioration in economic con-ditions, in the form of rainfall-related income shocks, contributes significantly toboth village- and country-level rates of HIV infection in sub-Saharan Africa. Whilethere are several possible pathways linking shocks to HIV, the available evidenceis inconsistent with all the potential pathways discussed here, except transactionalsex. Nonetheless, we have no conclusive evidence that transactional sex is indeed thepathway, and we cannot fully rule out that the other risk coping mechanisms dis-cussed, such as early marriage, school drop-out, or migration, are also contributingfactors.

Regardless of the pathway, the policy implications of these findings are substan-tial. If income shocks lead households to smooth income in ways that contributeto the epidemic, policies that prevent the need for these coping mechanisms wouldappear to yield large positive returns. Comprehensive social safety nets may unfor-tunately be an unrealistic short-run goal for many revenue and capacity-constrainedgovernments on the continent. However, more targeted interventions such as accessto credit and savings, weather-indexed crop insurance or the development of drought-resistant crop varieties could have an indirect affect on the spread of HIV by reducing


the sensitivity of incomes to rainfall shocks. Our results suggest that the social re-turns to investments in these and related interventions could be much larger thanpreviously thought, particularly in countries where HIV prevalence remains high.

81

Chapter 4

Quantifying the effect of climateon human conflict

4.1 Introduction*

Human behavior is complex, and despite the existence of institutions designed to pro-mote peace, interactions between individuals and groups sometimes lead to conflict.When such conflict becomes violent, it can have dramatic consequences on humanwellbeing. Mortality alone from war and interpersonal violence amounts to 0.5-1million deaths annually (Mathers, Boerma, and Ma Fat, 2008; Lozano et al., 2013),with non-lethal impacts including injury and lost economic opportunities affectingmillions more. Because the stakes are so high, understanding the causes of humanconflict has been a major project in the social sciences.

Researchers working across multiple disciplines including archaeology, criminol-ogy, economics, geography, history, political science, and psychology have long de-bated the extent to which climatic changes are responsible for causing conflict, vi-olence or political instability. Numerous pathways linking the climate to these out-comes have been proposed. For example, climatic changes may alter the supply ofa resource and cause disagreement over its allocation, or climatic conditions mayshape the relative appeal of using violence or cooperation to achieve some precon-ceived objective. Qualitative researchers have a well-developed history of studyingthese issues (Levy, 1995; Homer-Dixon, 1999; Scheffran et al., 2012b; Deligiannis,2012; Butzer, 2012) dating back at least to the start of the twentieth century (Hunt-

*This material is from joint authored work with Sol Hsiang and Ted Miguel that appeared inScience: “Quantifying the impact of climate on human conflict”, vol 341 no. 6151, 13 September2013. Reprinted here with permission from AAAS.

CHAPTER 4. CLIMATE AND CONFLICT 82

ington, 1917). Yet in recent years, growing recognition that the climate is changing,coupled with improvements in data quality and computing, have prompted an explo-sion of quantitative analyses seeking to test these theories and quantify the strengthof these previously proposed linkages. Thus far, this work has remained scatteredacross multiple disciplines and has been difficult to synthesize given the disparatemethodologies, data and interests of the various research teams.

Here we assemble the first comprehensive synthesis of this rapidly growing quanti-tative literature. We adopt a broad definition of “conflict”, using the term to encom-pass a range of outcomes from individual-level violence and aggression to country-level political instability and civil war. We then collect all available candidate studiesand – guided by previous criticisms that not all correlations imply causation (Hol-land, 1986; Gleditsch, 1998; Angrist and Steffen Pischke, 2010) – focus only on thosequantitative studies that can reliably infer causal associations (Holland, 1986; An-grist and Pischke, 2008) between climate variables and conflict outcomes. The studieswe examine exploit either experimental or natural-experimental variation in climate,where the latter term refers to variation in climate over time that is plausibly inde-pendent of other variables that also affect conflict. To meet this standard, studiesmust account for unobservable confounding factors across populations, as well as forunobservable time-trending factors that could be correlated with both climate andconflict (Wooldridge, 2002). In many cases we obtained data from studies that didnot meet this criteria and reanalyzed it using a common statistical model that metthis criteria (see Supplementary Online Material). The importance of this rigorousapproach is highlighted by an example where our standardized analysis generatedfindings consistent with other studies but at odds with the original conclusions ofthe study in question (Theisen, 2012).

In total, we obtained 60 primary studies that either met this criteria or werereanalyzed with a method that met this criteria (Table 1). Collectively, these stud-ies analyze 45 different conflict data sets published across 26 different journals andrepresent the work of over 190 researchers from around the world. Our evaluationsummarizes the recent explosion of research on this topic, with 78% of studies re-leased since 2009 and the median study released in 2011. We collect findings acrossa wide range of conflict outcomes, across time periods spanning 10,000 B.C.E to thepresent day, and across all major regions of the world (Fig. 1).

While various conflict outcomes differ in important ways, we find that the behav-ior of these outcomes relative to the climate system is remarkably similar. Put mostsimply, we find that large deviations from normal precipitation and mild tempera-tures systematically increase the risk of many types of conflict, often substantially,and that this relationship appears to hold over a variety of temporal and spatialscales. Our meta-analysis of studies that examine populations in the post-1950 era


Figure 4.1: Spatial and temporal coverage of the studies we review.

site

municipal

pixel

province

country

region

global

Spat

ial s

cale

of d

epen

dent

var

iabl

e

hour

day

week

mon

th

year

deca

de

cent

ury

mille

nnia

Duration of climatic event (log scale)

Hsiang et al.(2011)

8000 BCE 0 1000 1800 1950 2000 2010Years in study (log scale)

Kuper &Kröepelin

(2006)

Vrij et al. (1994)

N=9

Africa

Americas

Eurasia &Australia

Global

D’Angou et al.(2012)

58 out of 61 quantitative studies find a substantial intertemporal association between cli-matic variables and human conflict. Left panel: The location of each study region (y-axis)against the period of time included in the study (x-axis). Because multiple observationsare required for analysis, only studies that begin before 1950 are able to examine climaticchanges lasting decades or longer. The x-axis is scaled according to log years before presentbut labeled according to the year of the Common Era. Right panel: The level of aggregationin social outcomes (y-axis) against the timescale of climatic events (x-axis). The envelopeof spatial and temporal scales where associations are documented is shaded, with studiesat extreme vertices labeled for reference. Marker size denotes the number of studies ateach location, with the smallest bubbles marking individual studies and the largest bubblemarking nine studies.


suggest that these relationships continue to be highly significant in the modern world– although there are important differences in the magnitude of the relationship whendifferent variables are considered: the standardized effect of temperature is generallylarger than the standardized effect of rainfall and the effect on intergroup violence(e.g. civil war) is larger than the effect on interpersonal violence (e.g. assault).We conclude that there is substantially more agreement and generality in the find-ings of this burgeoning literature than has been previously recognized. Given thelarge potential changes in precipitation and temperature regimes projected in comingdecades, our findings have important implications for the social impact of anthro-pogenic climate change in both low- and high-income countries.

4.2 Estimation of climate-conflict linkages

Reliably measuring an effect of climatic conditions on human conflict is complicatedby the inherent complexity of social systems. In particular, a central concern iswhether statistical relationships can be interpreted causally or if they are confoundedby omitted variables. To address this concern, we restrict our attention to studieswith research designs that are a scientific experiment or that approximate one (i.e.“natural experiments”). After describing how studies meet this criteria, we discusshow we interpret the precision of results, how we assess the “importance” of climaticfactors, and how we address choices over functional form.

Research design

In an ideal experiment, we would observe two identical populations, change the cli-mate of one, and observe whether this “treatment” lead to more or less conflictrelative to the “control” conditions. Because the climate cannot be experimentallymanipulated, researchers primarily rely on natural experiments where a given pop-ulation is compared to itself at different moments in time when it is exposed todifferent climatic conditions – conditions which are exogenously determined by theclimate system (Holland, 1986; Freedman, 1991). In this research design, a singlepopulation serves as both the “control” population – e.g. just before a change inclimatic conditions– and the “treatment” population – e.g. just after a change in cli-matic conditions. Inferences are thus based only on how a fixed population respondsto different climatic conditions which vary over time, and time-series or longitudinalanalysis is used to construct a credible estimate for the causal effect of climate onconflict (Freedman, 1991; Angrist and Pischke, 2008; Greene, 2003).


To minimize statistical bias and to improve the comparability of studies, we focuson studies that use versions of the general model

conflict variableit = β × climate variableit + µi + θt + εit (4.1)

where locations are indexed by i, observational periods are indexed by t, β is theparameter of interest and ε is the error. If different locations in a sample exhibitdifferent average levels of conflict – perhaps because of cultural, historical, political,economic, geographic or institutional differences between the locations – this willbe accounted for by the location-specific constants µ (commonly known as “fixedeffects”). Time-specific constants θ (a dummy for each time period) flexibly accountfor other time-trending variables such as economic growth or gradual demographicchanges that could be correlated with both climate and conflict. In some cases,such as in time series, the θt parameters may be replaced by a generic trend (eg.θ × t) which is possibly nonlinear and is either common to all locations or may belocation-specific (eg. θi × t). Our conclusions from the literature are based onlyon those studies that implement Eq. 4.1 or one of the mentioned alternatives. Inselect cases, when studies did not meet this criteria but the data from these analyseswere publicly available or supplied by the authors, we reanalyzed the data usingthis common method (see SOM). Many estimates of Eq. 4.1 in the literature andin our reanalysis account for temporal and/or spatial autocorrelation in the errorterm ε, although this adjustment was not considered a requirement for inclusionhere. In the case of some paleoclimatological/archeological studies, formal statisticalanalysis is not implemented because the outcome variables of interest are essentiallysingular cataclysmic events; however, we include these studies because they followpopulations over time at a fixed location and are thus implicitly using the model inEq. 4.1 (these cases are noted in Table 1).

We do not consider studies that are purely cross-sectional, i.e. studies that onlycompare rates of conflict across different locations and that attribute differences inaverage levels of conflict to average climatic conditions. There are many ways inwhich populations differ from one another (culture, history, etc.), many of them un-observed, and these “omitted variables” are likely to confound these analyses. Inthe language of the natural experiment, the “treatment” and “control” populationsin these analyses are not comparable units, so we cannot infer whether a climatic“treatment” has a causal effect or not (Freedman, 1991; Greene, 2003; Gelman andHill, 2006; Wooldridge, 2002; Angrist and Pischke, 2008). For example, a cross-sectional study might compare average rates of civil conflict in Norway and Nigeria,attributing observed differences to the different climate of these countries – despitethe fact that there are clearly many other relevant ways in which these countriesdiffer. Nonetheless, some studies use cross-sectional analyses and attempt to control


for confounding variables in regression analyses, typically using a handful of covari-ates such as average income or political indices. However, because the full suite ofdeterminants of conflict are unknown and unmeasured, it is likely impossible thatany cross-sectional study can explicitly account for all important differences betweenpopulations. Rather than presuming that all confounders are accounted for, the stud-ies we evaluate only compare Norway or Nigeria to themselves at different momentsin time, thereby ensuring that the structure, history and geography of comparisonpopulations are nearly identical.

Some studies implement versions of Eq. 4.1 that are expanded to explicitly “con-trol” for potential confounding factors, such as average income. In many cases thisapproach is more harmful than helpful because it introduces bias in the coefficientsdescribing the effect of climate on conflict. This problem occurs when researcherscontrol for variables that are themselves affected by climate variation, causing either(i) the signal in the climate variable of interest to be inappropriately absorbed bythe “control” variable, or (ii) the estimate to be biased because populations differ inunobserved ways that become artificially correlated with climate when the “control”variable is included. This methodological error is commonly termed “bad control”(Angrist and Pischke, 2008) and we exclude results obtained using this approach.The difficulty in this setting is that climatic variables affect many of the socioeco-nomic factors commonly included as control variables - things like crop production,infant mortality, population (via migration or mortality), and even political regimetype. To the extent that these outcome variables are used as controls in Eq. 4.1,studies might draw mistaken conclusions about the relationship between climate andconflict. Because this error is so salient in the literature, we provide examples be-low. A full treatment can be found in refs. (Angrist and Krueger, 1999; Angrist andPischke, 2008).

For an example of (i), consider whether variation in temperature increases con-flict. In many studies of conflict, researchers often employ a “standard” set of controlswhich are correlates of conflict, such as per capita income. However, evidence sug-gests that income is itself affected by temperature (Schlenker and Roberts, 2009b;Hsiang, 2010; Dell, Jones, and Olken, 2012b), so if part of the effect of temperatureon conflict is through income, then “controlling” for income in Eq. 4.1 will lead theresearcher to underestimate the role of temperature in conflict. This occurs becausemuch of the effect of temperature will be absorbed by the income variable, biasingthe temperature coefficient toward zero. At the extreme, if temperature influencesconflict only through income, then controlling for income would lead the researcherin this example to draw exactly the wrong conclusion about the relationship betweentemperature and conflict: that there is no effect of temperature on conflict.

For an example of (ii), imagine that a measure of “politics” and temperature both


have a causal effect on conflict and that both politics and temperature have an effecton income, but that income has no effect on conflict. If politics and temperature areuncorrelated, estimates of Eq. 4.1 that do not control for politics will still recoverthe unbiased effect of temperature. However, If income is introduced to Eq. 4.1 as a“control” while politics is left out of the model, perhaps because it is more difficultto measure, then it will appear as if there is an association between income andconflict because income will be serving as a proxy measure for politics. In addition,this adjustment to Eq. 4.1 also biases the estimated effect of temperature. This biasoccurs because the types of countries that have high income when temperature ishigh are different, in terms of their average politics, than those countries that havehigh income when temperature is low. Thus, if income is “held fixed” as a controlvariable in a regression model, the comparison of conflict across temperatures isnot an apples-to-apples comparison because politics will be systematically differentacross countries at different temperatures, generating a bias that can have eithersign. In this example, the inclusion of income in the model leads to two incorrectconclusions: it biases the estimated relationship between climate and conflict and itimplicates income as playing a role in conflict when it does not.

Statistical precision

We consider each study’s estimated relationship between climate and conflict aswell as the estimate’s precision. Because sampling variability and sample sizes differacross studies, some analyses present results that are more precise than other studies.Recognizing this fact is important when synthesizing a diverse literature, as someapparent differences between studies can be reconciled by evaluating the uncertaintyin their findings. For example, some studies report associations that are very largeor very small but with uncertainties that are also very large, leading us to placeless confidence in these extreme findings. This intuition is formalized in our meta-analysis which aggregates results across studies by down-weighting results that areless precisely estimated.

The strength of a finding is sometimes summarized in a statement regarding its“statistical significance,” which describes the signal-to-noise ratio in an individualstudy. However, in principle the “signal” is a relationship that exists in the real worldand cannot be affected by the researcher, whereas the level of “noise” in a givenstudy’s finding (i.e. its uncertainty) is a feature specific to that study – a featurethat can be affected by a researcher’s decisions, such as the size of the sample theychoose to analyze. Thus, while it is useful to evaluate whether individual findings arestatistically significant and it is important to down-weight highly imprecise findings,


individual studies provide useful information even when they are not statisticallysignificant.

To summarize the evidence that each statistical study provides while also takinginto account its precision, we separately consider three questions for each study inTable 1: (1) Is the estimated average effect of climate on conflict quantitatively“large” in magnitude (discussed below), regardless of its uncertainty? (2) Is thereported effect large enough and estimated with sufficient precision that the studycan reject the null hypothesis of “no relationship” at the 5% level? (3) If the studycannot reject the hypothesis of “no relationship,” can it reject the hypothesis thatthe relationship is quantitatively large? In the literature, often only question 2 isevaluated in any single analysis. Yet it is important to consider the magnitudeof climate influence (question 1) separately from its statistical precision because themagnitude of these effects tell us something about the potential importance of climateas a factor that may influence conflict, so long as we are mindful that evidence isweaker if a study’s results are less certain. In cases where the estimated effect issmaller in magnitude and not statistically different than zero, it is important toconsider whether a study provides strong evidence of zero association – i.e. thestudy rejects the hypothesis that an effect is large in magnitude (question 3) – orrelatively weak evidence because the estimated confidence interval spans large effectsas well as spanning zero effect.

Evaluating if an effect is “important”

Evaluating whether an observed causal relationship is “important” is a subjectivejudgement that is not essential to our scientific understanding of whether there is acausal relationship. Nonetheless, because “importance” in this literature has some-times been incorrectly conflated with statistical precision or inferred from incorrectinterpretations of Eq. 4.1 and its variants, we explain our approach to evaluatingimportance.

Our preferred measure of importance is to ask a straightforward question: Dochanges in climate cause changes in conflict risk that an expert, policy-maker orcitizen would consider large? To aid comparisons, we operationalize this questionby considering an effect important if authors of a particular study state the size ofthe effect is substantive, or if the effect is greater than a 10% change in conflictrisk for each 1 standard deviation (1σ) change in climate variables. This secondcriteria uses an admittedly arbitrary threshold, and other threshold selections wouldbe justifiable. However, we contend this threshold is relatively conservative sincemost policy-makers or citizens would be concerned by effects well below 10%/σ. Forinstance, since random variation in a normally distributed climate variable lies in a


4σ range for 95% of its realizations, even a 3%/σ effect size would generate variationin conflict of 12% of its mean, which is probably important to those individualsexperiencing these shifts.

In some prior studies, authors have argued that a particular estimated effect is“unimportant” based on whether a climatic variable substantially changes goodness-of-fit measures (e.g. R2) for a particular statistical model, sometimes in comparisonto other predictor variables (Buhaug, 2010b; O’Loughlin et al., 2012; Theisen, 2012;Theisen, Holtermann, and Buhaug, 2011). We do not use this criteria here for tworeasons. First, goodness-of-fit measures are sensitive to the quantity of noise ina conflict variable: more noise reduces goodness-of-fit – thus, under this metric,irrelevant measurement errors that introduce noise into conflict data will reduce theapparent “importance” of climate as a cause of conflict, even if the effect of climate onconflict is quantitatively large. Second, comparing the goodness-of-fit across multiplepredictor variables often makes little sense in many contexts since (i) longitudinalmodels typically compare variables that predict both where a conflict will occurand when a conflict occur and (ii) these models typically compare the causal effectof climatic variables with the non-causal effects of confounding variables, such asendogenous covariates. These are apples-to-oranges comparisons and the faulty logicof both types of comparison are made clear with examples.

For an example of (i), consider an analyst comparing violent crime over timein New York City and North Dakota who finds that the number of police on thestreet each day are important for predicting how much crime occurs on that day, butthat a population variable describes more of the variation in crime since crime andpopulation in North Dakota are both low. Clearly this comparison is not informative,since the reason that there is little crime in North Dakota has nothing to do withthe reason why crime is lower in New York City on days when there are manypolice on the street. The argument that variations in climate are “not important” topredicting when conflict occurs because other variables are good predictors of whereconflict occurs is analogous to the strange statement that the number of police inNew York City are “not important” for predicting crime rates because North Dakotahas lower crime that is attributable to its lower population.

For an example of (ii), suppose that both higher rainfall and higher householdincome lower the likelihood of civil conflict, but household income is not observedand instead a variable describing the average observable number of cars each house-hold owns is included in the regression. Because wealthier households are better ableto afford cars, the analyst finds that populations with more cars have a lower riskof conflict. This relationship clearly does not have a causal interpretation and com-paring the “effect of car ownership on conflict” with the effect of rainfall on conflictdoes not help us better understand the importance of the rainfall variable. Published


studies that make similar comparisons do so with variables that the authors suggestare more relevant than cars, but the uninformative nature of comparisons betweencausal effects and non-causal correlations is the same.

Functional form and evidence of nonlinearity

Some studies assume a linear relationship between climatic factors and conflict risk,while others assume a non-linear relationship. Taken as a whole, the evidence sug-gests that over a sufficiently large range of temperatures and rainfall levels, bothtemperature and precipitation appear to have a non-linear relationship with conflict,at least in some contexts. However, this curvature is not apparent in every study,probably because the range of temperatures or rainfall levels contained within asample may be relatively limited. Thus, most studies report only linear relationshipsthat should be interpreted as local linearizations of a more complex – and possiblycurved – response function.

As we will show, all modern analyses that address temperature impacts find thathigher temperatures lead to more conflict. However, a few historical studies thatexamine temperate locations during cold epochs do find that abrupt cooling from analready cold baseline temperature may lead to conflict. Taken together, this collec-tion of locally linear relationships indicates a global relationship with temperaturethat is non-linear.

In studies of rainfall impacts, the distinction between linearity and curvature ismade fuzzy by the multiple ways that rainfall changes have been parameterized inexisting studies. Not all studies use the same independent variable, and because asimple transformation of an independent variable can change the response functionfrom curved to linear and visa versa, this makes it difficult to determine whetherresults agree. In an attempt to make findings comparable, when replicating thestudies that originally examine a non-linear relationship between rainfall and conflictwe follow the approach of Hidalgo et al. (Hidalgo et al., 2010b) and use the absolutevalue of rainfall deviations from the mean as the independent variable; in studies thatoriginally examined linear relationships we leave the independent variable unaltered.Because these two approaches in the literature (and our reanalysis) differ, we makethe distinction clear in our figures through the use of two different colors.

4.3 Results from the quantitative literature

We divide our review topically, examining in turn the evidence on how climaticchanges shape personal violence, group-level violence, and the breakdown of social


order and political institutions. Results from twelve example studies of recent data(post-1950) are displayed in Fig. 2, which we replicated using the common statisticalframework described above, and which were chosen to represent a broad cross sectionof outcomes, geographies, and time periods (see SOM).1 Findings from several studiesof historical data are collected in Fig. 3, where the different time scales of climaticevents can be easily compared. A listing and description of all primary studies arein Table 1. For a detailed description and evaluation of each individual study, werefer readers to ref. (Hsiang and Burke, in press).

Personal violence and crime

Studies in psychology and economics have repeatedly found that subjects are morelikely to exhibit aggressive or violent behavior towards others if ambient temperaturesat the time of observation are higher (Fig. 2A, B, C), a result that has been obtainedin both experimental (Kenrick and Macfarlane, 1986; Vrij, der Steen, and Koppelaar,1994) and natural-experimental (Auliciems and DiBartolo, 1995; Cohn and Rotton,1997; Rotton and Cohn, 2000; Bushman, Wang, and Anderson, 2005; Anderson,Bushman, and Groom, 1997; Anderson et al., 2000; Jacob, Lefgren, and Moretti,2007; Larrick et al., 2011; Card and Dahl, 2011; Ranson, 2012; Mares, 2013) settings.Documented aggressive behaviors that respond to temperature range from somewhatless consequential – e.g. horn-honking while driving (Kenrick and Macfarlane, 1986)and inter-player violence during sporting events (Larrick et al., 2011) – to much moreserious – e.g. the use of force during police training (Vrij, der Steen, and Koppelaar,1994), domestic violence within households (Auliciems and DiBartolo, 1995; Cardand Dahl, 2011), and violent crimes such as assault or rape (Cohn and Rotton, 1997;Rotton and Cohn, 2000; Bushman, Wang, and Anderson, 2005; Anderson, Bushman,and Groom, 1997; Anderson et al., 2000; Jacob, Lefgren, and Moretti, 2007; Ranson,2012). Although the physiological mechanism linking temperature to aggressionremains unknown, the causal association appears robust across a variety of contexts.Importantly, because aggression at high temperature increases the likelihood that

1In Figure 2, both dependent and independent variables have had location-effects and trendsremoved, so all samples have a mean of zero. Non-parametric “watercolor regressions” where thecolor intensity of 95% confidence intervals depicting the likelihood that the true regression linepasses through a given value (darker is more likely) (Hsiang, 2013). White line is the conditionalmean. Climate variables are indicated by color: red = temperature, green = rainfall deviationsfrom normal, blue = precipitation loss, black = ENSO. Panel titles describe the outcome variable,location, unit of analysis, sample size and study. “Rainfall deviation” describes the magnitude oflocation-specific rainfall anomalies, with both abnormally high and abnormally low rainfall eventsare both described as having a large rainfall deviation. “Precipitation Loss” describes how muchlower precipitation is relative to the prior year or long-term mean.


Figure 4.2: Examples from studies of modern data.

See text for a description of what is shown in the plots.


intergroup conflicts escalate in some contexts (Larrick et al., 2011) and the likelihoodthat police officers use force (Vrij, der Steen, and Koppelaar, 1994), it is possible thatthis mechanism could affect the prevalence of larger scale group-level conflicts.

In low-income settings, extreme rainfall events that adversely affect agriculturalincome are also associated with higher rates of personal violence (Miguel, 2005; Sekhriand Storeygard, 2012; Blakeslee and Fishman, 2013) and property crime (Mehlum,Miguel, and Torvik, 2006). High temperatures are also associated with increasedproperty crime (Anderson et al., 2000; Jacob, Lefgren, and Moretti, 2007; Ranson,2012), but violent crimes appear to rise with temperature more quickly than propertycrimes (Ranson, 2012).

Group-level violence and political instability

Some forms of intergroup violence, such as Hindu-Muslim riots (Fig. 2D), tend tobe more likely following extreme rainfall conditions (Bohlken and Sergenti, 2010;Sarsons, 2011; Hendrix and Salehyan, 2012; Kung and Ma, 2012). This relation-ship between intergroup violence and rainfall is primarily documented in low-incomesettings, suggesting that reduced agricultural production may be an important me-diating mechanism – although alternative explanations cannot be excluded.

Low water availability (Miguel, Satyanath, and Sergenti, 2004b; Levy et al., 2005;Bai and Kung, 2010; Hsiang, Meng, and Cane, 2011; Harari and La Ferrara, 2013;Couttenier and Soubeyran, 2013; Hendrix and Salehyan, 2012; Cervellati, Sunde, andValmori, 2011; O’Loughlin et al., 2012; Fjelde and von Uexkull, 2012; Jia, 2013; Leeet al., 2013), very low temperatures (Zhang et al., 2006, 2007; Tol and Wagner, 2010;Zhang et al., 2011; Buntgen et al., 2011; Anderson, Johnson, and Koyama, 2013)and very high temperatures (Burke et al., 2009a; Hsiang, Meng, and Cane, 2011;Dell, Jones, and Olken, 2012b; Theisen, 2012; O’Loughlin et al., 2012; Almer andBoes, 2012; Maystadt, Ecker, and Mabiso, 2013) have been associated with organizedpolitical conflicts in a variety of low-income contexts (Fig. 2 E, F, H, I, K, L). Thestructure of this relationship again seems to implicate a pathway through climate-induced changes in income, either agricultural (Miguel, Satyanath, and Sergenti,2004b; Schlenker and Roberts, 2006; Schlenker and Lobell, 2010a; Lobell and Burke,2010) or non-agricultural (Hsiang, 2010; Dell, Jones, and Olken, 2012b), althoughthis hypothesis remains speculative. Large deviations from normal precipitation havealso been shown to lead to the forceful reallocation of wealth (Hidalgo et al., 2010b)(Fig. 2G) or the non-violent replacement of incumbent leaders (Chaney, 2011; Burke,2012) (Fig. 2J).

Some authors recently suggested that contradictory evidence is widespread amongquantitative studies of climate and human conflict (Scheffran et al., 2012a; Gleditsch,


2012; Bernauer, Bohmelt, and Koubi, 2012), but the level of disagreement appearsoverstated. Two studies (Buhaug, 2010b; Theisen, Holtermann, and Buhaug, 2011)estimate that temperature and rainfall events have a limited impact on civil war inAfrica, but the confidence intervals around these estimates are sufficiently wide thatthey do not reject a relatively large effect of climate on conflict that is consistent with35 other studies of modern data and 28 other studies of inter-group conflict. Withinthe broader literature of primary statistical studies, these results represent 4% ofall reported findings (Table 1). Isolated studies also suggest that windstorms andfloods have limited observable effect on civil conflicts (Bergholt and Lujala, 2012)and that anomalously high rainfall is associated with higher incidence of terroristattacks (Salehyan and Hendrix, 2012).

Institutional breakdown

Under sufficiently high levels of climatological stress, pre-existing social institutionsmay strain beyond recovery and lead to major changes in governing institutions(Burke and Leigh, 2010; Bruckner and Ciccone, 2011; Yancheva et al., 2007) (Fig.3C), a process that often involves the forcible removal of rulers. High levels of cli-matological stress have also led to major changes in settlement patterns and socialorganization (DeMenocal, 2001; Kuper and Kropelin, 2006) (Fig. 3D). Finally, in ex-treme cases, entire communities, civilizations and empires collapse entirely followinglarge changes in climatic conditions (Stahle et al., 1998; Cullen et al., 2000; DeMeno-cal, 2001; Haug et al., 2003; Yancheva et al., 2007; Buckley et al., 2010; Pattersonet al., 2010; Buntgen et al., 2011; Kennett et al., 2012; Kelly et al., 2013; D’Anjouet al., 2012) (Fig. 3 A-C, E-F). These documented catastrophic failures all precedethe twentieth century, yet the level of economic development in these communities atthe time of their collapse was similar to the level of development in many poor coun-tries of the modern world (see ref. (Hsiang and Burke, in press) for a comparison),an indicator that these historical cases may continue to have modern relevance.

4.4 Synthesis of findings

Once attention is restricted to those studies able to make rigorous causal claimsabout the relationship between climate and conflict, some general patterns becomeclear. Here we identify, for the first time, commonalities across results that spandiverse socials systems, climatological stimuli and research disciplines.


Figure 4.3: Examples of paleoclimate reconstructions that find associationsbetween climatic changes and human conflict

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Dark lines are climate reconstructions (smoothed moving averages when grey lines areshown), and orange shaded areas indicate periods of substantial social instability, violentconflict, or the breakdown of political institutions.


Generality: samples, spatial scales, and rates of climatechange

Social conflicts at all scales and levels of organization appear susceptible to climaticinfluence, and multiple dimensions of the climate system are capable of influencingthese various outcomes. Studies documenting this relationship can be found in datasamples covering 10,000 BCE to the present and this relationship has been identifiedmultiple times in each major region, as well as in multiple samples with globalcoverage (Fig. 1A).

Climatic influence on human conflict appears in both high and low income so-cieties, although some types of conflict, such as civil war, are rare in high incomepopulations do not exhibit a strong dependance on climate in those regions (Hsiang,Meng, and Cane, 2011). Nonetheless, many other forms of conflict in high incomecountries such as violent crime (Jacob, Lefgren, and Moretti, 2007; Ranson, 2012),police violence (Vrij, der Steen, and Koppelaar, 1994), or leadership changes (Burke,2012), do respond to climatic changes. These forms of conflict are individually lessextreme, but their total social cost may be large because they are widespread. Forexample, during 1979-2009 there were more than two million violent crimes (assault,murder and rape) per year on average in the United States alone (Ranson, 2012), sosmall percentage changes can lead to substantial increases in the absolute number ofthese types of events.

Climatic perturbations at spatial scales ranging from a building (Vrij, der Steen,and Koppelaar, 1994; Kenrick and Macfarlane, 1986; Larrick et al., 2011) to the globe(Hsiang, Meng, and Cane, 2011) have been found to influence human conflict or socialstability (Fig. 1B). The finding that climate influences conflict across multiple scalessuggests that coping or adaptation mechanisms are often limited. Interestingly, asshown in Fig. 1B, there is a positive association between the temporal and spatialscales of observational units in studies documenting a climate-conflict link. Thismight indicate that larger social systems are less vulnerable to high frequency climateevents, or it may be that higher-frequency climate events are more difficult to detectin studies examining outcomes over wide spatial scales.

Finally, it is sometimes argued that societies are particularly resilient to climateperturbations of a specific temporal scale – perhaps they are capable of bufferingthemselves against short-lived climate events, or alternatively that they are able toadapt to conditions that are persistent. With respect to human conflict, the availableevidence does not support either of these claims. Climatic anomalies of all temporaldurations, from the anomalous hour (Vrij, der Steen, and Koppelaar, 1994) to theanomalous millennium (Kuper and Kropelin, 2006), have been implicated in someform of human conflict (Fig. 1B).


The association between climatic events and human conflict is general in thesense that it has been observed almost everywhere: across types of conflict, acrosshuman history, across regions of the world, across income groups, across the variousdurations of climatic changes, and across all spatial scales. However, it is not truethat all types of climatic events influence all forms of human conflict or that climaticconditions are the sole determinant of human conflict. The influence of climate isdetectable across contexts, but we strongly emphasize that it is only one of manyfactors that contribute to conflict (see ref. (Blattman and Miguel, 2010) for a reviewof these other factors).

The direction and magnitude of climatic influence on humanconflict

We must consider the magnitude of the climate’s influence in order to evaluatewhether climatic events play an important role in the occurrence of conflict, andwhether anthropogenic climate change has the potential to substantially alter futureconflict outcomes. Quantifying the magnitude of climatic impact in archeological/paleo-climatological studies is difficult because outcomes of interest are often one-off cat-aclysmic events (e.g. societal collapse) and we typically do not observe how theuniverse of societies would have responded to similar sized shocks. Modern datasamples, however, generally contain a large number of comparable social units (e.g.,countries) that are repeatedly exposed to climatic variation, and this setting thatis more amenable to statistical analyses that quantify how changes in climate affectthe risk of conflict within an individual social unit.

To compare quantitative results across studies of modern data, we computedstandardized effect sizes for those studies where it was possible to do so, evaluatingthe effect of a 1σ change in the explanatory climate variable and expressing the resultas a percentage change in the outcome variable. Because we restrict our attention tostudies that examine changes in climate variables over time, the relevant standarddeviation is based only on inter-temporal changes at each specific location instead ofcomparing variation in climate across different geographic locations.

Our results are displayed in Fig. 4-5 (colors match Fig. 2-3). Nearly all stud-ies suggest that warmer temperatures, lower or more extreme rainfall, or warmerEl Nino-Southern Oscillation (ENSO) conditions lead to a 2-40% increase in theconflict outcome per 1σ in the observed climate variable. The consistent directionof temperature’s influence is particularly remarkable since all 27 modern estimates(including ENSO and temperature-based drought indices, 20 estimates are shownin Fig. 4-5) indicate that warmer conditions generate more conflict, a result that


would be extremely unlikely to occur by chance alone if temperature had no effect onconflict. It is more difficult to interpret whether the sign of rainfall-related variablesagree because these variables are parametrized several different ways, so Fig. 4-5present likelihoods for different parameterizations separately. However, if all modernrainfall estimates are pooled (including ENSO and rainfall-based drought indices, 13estimates are shown in Fig. 4-5) using signs shown in Fig. 4-5, then the sign of theeffect in 17 out of 19 estimates agree.

Under the assumption that there is some underlying similarity across studies,we compute the average effect of climate variables across studies by weighting eachestimate according to its precision (the inverse of the estimated variance), a com-mon approach that penalizes uncertain estimates (Hedges and Olkin, 1985). Wealso calculate the confidence interval on this mean by assuming independence acrossstudies, although this assumption is not critical to our central findings (in the SOMwe present results where we relax this assumption and show that it is not essential).The precision-weighted average effect on interpersonal conflict is a 2.3% increase foreach 1σ change in climatic variables (s.e.= 0.12%, p <0.001, Fig. 4 and Table S1)and the analogous estimate for intergroup conflict is 11.1% (s.e.= 1.3%, p <0.001,Fig. 5 and Table S1). These precision-weighted averages are relatively un-influencedby outliers since outlier estimates in our sample tend to have low precision and thuslow weight in the meta-analysis. The corresponding medians, which are also insen-sitive to outliers, are comparable: 3.9% for personal conflict and 13.6% for groupconflict. If we restrict our attention to only the effects of temperature, the precision-weighted average effect is similar for interpersonal conflict (2.3%), but for intergroupconflict rises to 13.2% per 1σ in temperature (s.e.= 2.0, p < 0.001, Fig. 5). Re-garding the interpretation of these effect sizes, we note that while the average effectfor interpersonal violence is smaller than the average effect for intergroup conflictin percentage terms, the baseline number of incidents of interpersonal violence isdramatically higher, meaning a small percentage increase can represent a substantialincrease in total incidents.

We estimate the precision-weighted probability distribution of study-level effect-sizes in Fig. 4-5 and in Table S1. These distributions are centered at the precision-weighted averages described above and can be interpreted as the distribution ofresults from which studies’ findings are drawn. The distribution for interpersonalconflict is narrow around its mean, likely because most interpersonal conflict studiesfocus on one country (the United States) and use very large samples and derivevery precise estimates. The distribution for intergroup conflict is broader and coversvalues that are larger in magnitude, with an interquartile range 6 to 14% per 1σ andthe 5-95th percentiles spanning -5 to 32% per 1σ (Table S1). We estimate that forthe intergroup and interpersonal conflict studies, respectively, 10% and 0% of the

CHAPTER 4. CLIMATE AND CONFLICT 99F

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−8−404812

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Ranson 2012

Larrick et al 2011

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Sekhri and Storeygard 2012

Auliciems and DiBartolo 1995

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probability mass of the distributions of effect sizes lies below zero.Fig. 4-5 make it clear that even though there is substantial agreement across

results, some heterogeneity across estimates remains. It is possible that some of thisvariation is meaningful, perhaps because different types of climate variables havedifferent impacts or because the social, economic, political or geographic conditionsof a society mediate its response to climatic events. For instance, poorer populationsappear to have larger responses, consistent with prior findings that such populationsare more vulnerable to climatic shifts (Hsiang, Meng, and Cane, 2011). However,it is also possible that some of this variation is due to differences in how conflictoutcomes are defined, to measurement error in climate variables, or to remainingdifferences in model specifications that we could not correct in our reanalysis.

To formally characterize the variation in estimated responses across studies, weuse a Bayesian hierarchical model that does not require knowledge of the sourceof between-study variation (Gelman et al., 2004) (see SOM). Under this approach,estimates of the precision-weighted mean are essentially unchanged, and we recoverestimates for the between-study standard deviation (a measure of the underlyingdispersion of “true” effect sizes across studies) that are half of the precision-weightedmean for interpersonal conflict, and two-thirds of the precision-weighted mean forintergroup conflict (median estimates; see SOM, Fig. S3 and Tables S2-S3). Bycomparison, if variation in effect sizes across studies was driven by sampling variationalone, then this standard deviation in the underlying distribution of effect sizes wouldbe zero. This suggests “true” effects likely differ across settings, and understandingthis heterogeneity should be a primary goal of future research.

Publication bias

Publication bias is a longstanding concern across the sciences, with a common formof bias arising from the research community’s perceived preference for positive ratherthan null results. Although it is always possible that publication bias played a rolein the publication of a specific analysis, there are multiple reasons why publicationbias is unlikely to be driving our findings about the literature on climate and conflict.First, we include working papers in our analysis (as is common practice in the socialsciences), thereby eliminating editorial selection. Second, the central results pre-sented here are replicated in multiple disciplines and across diverse samples. Third,the large number of positive findings present in the literature since 2009 could providelimited professional incentive for researchers to publish yet another positive finding,and benefits might be higher to those who publish results with alternative findings.Fourth, many analyses are not explicitly focused on the direct effect of climate onconflict but instead use climatic variations instrumentally (Miguel, Satyanath, and


Sergenti, 2004b; Jacob, Lefgren, and Moretti, 2007; Hidalgo et al., 2010b; Burke,2012; Burke and Leigh, 2010) or account for it as an ancillary covariate in their anal-ysis (e.g. (Card and Dahl, 2011)) while trying to study a different research question– indicating that these authors have little professional stake in the sign, magnitudeor statical significance of the climatic effects they are presenting. Fifth, we reana-lyze the raw data from many studies using a common statistical framework, possibly“undoing” adjustments that authors might be making to their analysis (consciouslyor unconsciously) that make their findings appear stronger – partial support for thisidea is provided by individual studies that present significant results, but whose re-sults are only marginally significant or no longer significant after our reanalysis (seeSOM for details). Finally, we look for evidence of publication bias by examiningwhether the statistical strength of individual studies reflects their sample size (Cardand Krueger, 1995) and do not find systematic evidence of strong bias in absoluteterms or in comparison to other social science literatures (see Fig. S4, Table S4, andSOM).

4.5 Implications for future climatic changes

The above evidence makes a prima facie case that future anthropogenic climatechange could worsen conflict outcomes across the globe in comparison to a futurewith no climatic changes, given the large expected increase in global surface temper-atures and the likely increase in variability of precipitation across many regions overcoming decades (Meehl et al., 2007b; IPCC, 2012). Recalling our finding that a 1σchange in a location’s temperature is associated with an average 2.3% increase in therate of interpersonal conflict and a 13.2% increase in the rate of intergroup conflict,and assuming that future populations will respond to climatic shifts similarly to howcurrent populations respond, one can consider the potential effect of anthropogenicwarming by rescaling expected temperature changes according to each location’s his-torical variability. While not all conflict outcomes have been shown responsive tochanges in temperature, many have, and the results uniformly indicate that increas-ing temperatures are harmful in regions that are temperate or warm initially. In Fig.6 we plot expected warming by 2050, computed as the ensemble mean for 21 climatemodels running the A1B emissions scenario, in terms of location-specific standarddeviations (Meehl et al., 2007c). Almost all inhabited locations warm by > 2σ, withthe largest increases exceeding 4σ in tropical regions that are already warm andcurrently experience relatively low inter-annual temperature variability. These largeclimatological changes, combined with the quantitatively large effect of climate onconflict – particularly intergroup conflict – suggest that amplified rates of human


conflict could represent a large and critical impact of anthropogenic climate changeTwo reasons are often given as to why climate change might not have a substan-

tive impact on human conflict: future climate change will occur gradually and willthus allow societies to adapt, and the modern world today is less susceptible to cli-mate variation than it has been in the past. However, if slower-moving climate shockshave smaller effects, or if the world has become less climate sensitive, it is unfortu-nately not obvious in the data. Gradual climatic changes appear to adversely affectconflict outcomes, and the majority of the studies we review use a sample period thatextends into the 21st century (recall Fig. 1). Furthermore, some studies explicitlyexamine whether populations inhabiting hotter climates exhibit less conflict whenhot events occur, but find little evidence that these areas are more adapted (Rottonand Cohn, 2000; Ranson, 2012). We also note that many of the modern linkagesbetween high temperature anomalies and intergroup conflict have been character-ized in Africa (Burke et al., 2009a; Theisen, 2012; O’Loughlin et al., 2012; Harariand La Ferrara, 2013; Maystadt, Ecker, and Mabiso, 2013) or the global tropics andsubtropics (Hsiang, Meng, and Cane, 2011; Dell, Jones, and Olken, 2012b), regionswith hot climates where we would expect populations to be best adapted to hightemperatures. Nevertheless, it is always possible that future populations will adaptin previously unobserved ways, but it is impossible to know if and to what extentthese adaptations will make conflict more or less likely.

Studies of non-conflict outcomes do indicate that in some situations, historicaladaptation to climate is observable, albeit costly (Hornbeck, 2012b; Libecap andSteckel, 2011; Deschenes and Greenstone, 2011; Hsiang and Narita, 2012), while inother cases there is limited evidence that any adaptation is occurring (Schlenker andRoberts, 2009b; Burke and Emerick, 2013). To our knowledge, no study has char-acterized the scale or scope for adaptation to climate in terms of conflict outcomes,and we believe this is an important area for future research. Given the quantitativelylarge effect of climate on conflict, future adaptations will need to be dramatic if theyare to offset the potentially large amplification of conflict.

4.6 Future research

Given the remarkable consistency of available quantitative evidence linking climateand conflict, in our view the top research priority in this field should be to narrowthe number of competing explanatory hypotheses. Beyond efforts to mitigate futurewarming, limiting climate’s future influence on conflict requires that we understandthe causal pathways that generate the observed association. This task is made dif-ficult by the likely situation that multiple mechanisms contribute to the observed


Fig

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relationships and that different mechanisms dominate in different contexts. The richqualitative literature (Levy, 1995; Homer-Dixon, 1999; Scheffran et al., 2012b; Deli-giannis, 2012; Butzer, 2012) suggest that a multiplicity of mechanisms may be atwork.

To date, no study has been able to conclusively pin down the full set of causalmechanisms, although some studies find suggestive evidence that a particular path-way contributes to the observed association in a particular context. In most cases,this is accomplished by “fingerprinting” the effect of climate on an intermediary vari-able, such as income, and showing that the same statistical fingerprint is visible in theclimate’s effect on conflict. This approach – typically called “instrumental variables”(Angrist and Pischke, 2008) in the social sciences – identifies a mechanism linkingclimate and conflict under the assumption that climate’s only influence on conflict isthrough the particular intermediate variable in question. Because this assumption isoften difficult or impossible to test, evidence from this approach is more suggestivethan conclusive in uncovering mechanisms (Hsiang, Meng, and Cane, 2011).

An alternate and promising research design that can help rule out certain hy-potheses is to study situations where plausibly exogenous events block a proposedpathway in a “treated” subpopulation and then to compare whether the climate-conflict association persists or disappears in both the treatment and control subpop-ulations. An example of this approach, Sarsons (2011) examines whether rainfallshortages in India lead to riots because they depress local agricultural income (Sar-sons, 2011). By showing that rainfall shortages and riots continue to occur togetherin districts with dams that supply irrigation, investments that partially decouplelocal agricultural income from temporary rain shortfalls, Sarsons argues that therainfall effect on riots is unlikely to be operating solely through changes in localagricultural income.

Plausible mechanisms

The following hypotheses have, in our judgement, received the strongest empiricalsupport in existing analyses, although the evidence is still often inconclusive. A com-mon hypothesis focuses on local economic conditions and labor markets, and arguesthat when climatic events cause economic productivity to decline (Schlenker andLobell, 2010a; Hsiang, 2010; Lobell and Burke, 2010; Schlenker and Roberts, 2009b;Barrios, Bertinelli, and Strobl, 2010; Graff Zivin and Neidell, in press; Dell, Jones,and Olken, 2012b; Jones and Olken, 2010a), the value of engaging in conflict is likelyto rise relative to the value of participating in normal economic activities (Miguel,Satyanath, and Sergenti, 2004b; Dube and Vargas, 2013; Angrist and Kugler, 2008;Chassang and Padro-i-Miquel, 2009; Dal Bo and Dal Bo, 2011; Berman, Shapiro,


and Felter, 2011; Lei and Michaels, 2011; Harari and La Ferrara, 2013). A compet-ing hypothesis on state capacity argues that these declines in economic productivityreduce the strength of governmental institutions (e.g. if tax revenues fall), curtailingtheir ability to suppress crime and rebellion or encouraging competitors to initiateconflict during these periods of relative state weakness (Haug et al., 2003; Yanchevaet al., 2007; Burke, 2012; Burke and Leigh, 2010; Chaney, 2011; Buckley et al., 2010;Zhang et al., 2011; Bruckner and Ciccone, 2011).

A second set of hypotheses focus on what has more generally been termed “grievances”.Hypotheses about inequality contend that when climatic events increase actual (orperceived) social and economic inequalities in a society (Grove, 2007; Anttila-Hughesand Hsiang, 2012), this could increase conflict by motivating attempts to redistributeassets (Anderson et al., 2000; Mehlum, Miguel, and Torvik, 2006; Jacob, Lefgren, andMoretti, 2007; Hidalgo et al., 2010b). Evidence linking changes in food prices to con-flict (Lagi, Bertrand, and Bar-Yam, 2011; Zhang et al., 2011; Arezki and Bruckner,2011; Barrett, 2013) can be interpreted similarly – e.g. food riots due to a govern-ment’s perceived inability to keep food affordable – particularly when some membersof society can influence food markets (Grove, 2007; Carter and Bates, 2012).

Climate-induced migration and urbanization might also be implicated in con-flict. If climatic events cause large population displacements or rapid urbanization(Barrios, Bertinelli, and Strobl, 2006; Feng, Oppenheimer, and Schlenker, 2012b;Hornbeck, 2012b), this might lead to conflicts over geographically stationary re-sources that are unrelated to the climate (Jensen and Gleditsch, 2009) but becomerelatively scarce where populations concentrate. Changes in climate might also af-fect the logistics of human conflict (Salehyan and Hendrix, 2012; Fearon and Laitin,2003), for example by altering the physical environment (eg. road quality) in whichdisputes or violence might occur (Fearon and Laitin, 2003; Harari and La Ferrara,2013; Butler and Gates, 2012). Finally, climate anomalies might result in conflictbecause they can make cognition and attribution more difficult or error-prone, orthey many affect aggression through some physiological mechanism. For instance,climatic events may alter individuals’ ability to reason and correctly interpret events(Kenrick and Macfarlane, 1986; Vrij, der Steen, and Koppelaar, 1994; Cohn andRotton, 1997; Rotton and Cohn, 2000; Anderson et al., 2000; Larrick et al., 2011;Jacob, Lefgren, and Moretti, 2007), possibly leading to conflicts triggered by misun-derstandings. Alternatively, if climatic changes and their economic consequences areinaccurately attributed to the actions of an individual or group (Achen and Bartels,2004; Hibbs Jr, 2006; Healy, Malhotra, and Mo, 2010; Manacorda, Miguel, and Vig-orito, 2011; Anderson, Johnson, and Koyama, 2013), for example an inept politicalleader (Burke, 2012), this may lead to violent actions that try to return economicconditions to normal by removing the “offending” population.


Selecting climate variables and conflict outcomes

Climate variables that have been previously analyzed, such as seasonal temperatures,precipitation, water availability indices, and climate indices, may be correlated withone another and autocorrelated across both time and space. For instance, temper-ature and precipitation time-series tend to be negatively correlated in much of thetropics and drought indices tend to be spatially correlated (Hsiang, Meng, and Cane,2011; Auffhammer et al., 2013b). Unfortunately, only a few of the existing studiesaccount for the correlations between different variables, so it may be that some stud-ies mistakenly measure the influence of an omitted climate variable by proxy (seeref. (Auffhammer et al., 2013b) for a complete discussion of this issue). Except forthe experiments linking temperature to aggression (Vrij, der Steen, and Koppelaar,1994; Kenrick and Macfarlane, 1986), only a few studies demonstrate that a spe-cific climate variable is more important for predicting conflict than other climatevariables or that climatic changes during a specific season are more important thanduring other seasons. Furthermore, no study isolates a particular type of climaticchange as the most influential and no study has identified whether temporal or spa-tial autocorrelations in climatic variables are mechanistically important. Identifyingthe climatic variables, timing of events and forms of autocorrelation that influenceconflict will help us better understand the mechanisms linking climatic changes toconflict.

A similar situation exists with the choice of conflict outcomes. Most analysessimply document changes in the rate at which conflicts are reported in aggregate,but this approach provides only limited insight into how the evolution of conflict isimpacted by climatic variables. A path for future investigation is to link climate datawith richer conflict data that describes different stages of the conflict “lifecycle”. Forexample, future studies could examine how often non-violent group disputes becomeviolent. Two studies in this review (Vrij, der Steen, and Koppelaar, 1994; Larricket al., 2011) demonstrate the usefulness of selecting conflict-variables other than totalconflict rates. By examining the probability that an initial confrontation escalatesrather than just counting the total number of conflicts, these studies demonstratethat high temperatures lead to more violence by increasing the likelihood that asmall conflict escalates into a larger conflict.

4.7 Conclusion

Findings from a growing corpus of rigorous quantitative research across multiple dis-ciplines suggest that past climatic events have exerted significant influence on human


conflict. This influence appears to extend across the world, throughout history, andat all scales of social organization. We do not conclude that climate is the sole –or even primary – driving force in conflict, but we do find that when large climatevariations occur, they can have substantial effects on the incidence of conflict acrossa variety of contexts. The median effect of a 1σ change in climate variables generatesan 14% change in the risk of intergroup conflict and a 4% change in interpersonal vio-lence, across the studies that we review where it is possible to calculate standardizedeffects. If future populations respond similarly to past populations, then anthro-pogenic climate change has the potential to substantially increase conflict aroundthe world, relative to a world without climate change.

Although there is remarkable convergence of quantitative findings across disci-plines, many open questions remain. Existing research has successfully establisheda causal relationship between climate and conflict but is unable to fully explain themechanisms. This fact motivates our proposed research agenda and urges cautionwhen applying statistical estimates to future warming scenarios. Importantly, how-ever, it does not imply that we lack evidence of a causal association. The studiesin this analysis were selected for their ability to provide reliable causal inferencesand they consistently point toward the existence of at least one causal pathway. Toplace the state of this research in perspective, it is worth recalling that statisticalanalyses identified the smoking of tobacco as a proximate cause of lung cancer by the1930’s (Witschi, 2001), although the research community was unable to provide adetailed account of the mechanisms explaining the linkage until many decades later.So although future research will be critical in pinpointing why climate affects humanconflict, disregarding the potential effect of anthropogenic climate change on humanconflict in the interim is, in our view, a dangerously misguided interpretation of theavailable evidence.

Numerous competing theories have been proposed to explain the linkages be-tween the climate and human conflict, but none have been convincingly rejectedand all appear to be consistent with at least some existing results. It seems likelythat climatic changes influence conflict through multiple pathways that may differbetween contexts and innovative research to identify these mechanisms is a top re-search priority. Achieving this research objective holds great promise, as the policiesand institutions necessary for conflict resolution can only be built if we understandwhy conflicts arise. The success of such institutions will be increasingly importantin the coming decades as changes in climatic conditions amplify the risk of humanconflicts.


Tab

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dco

nflic

t,vio

lence

orp

olit

ical

inst

abilit

y

Stu

dy

Sam

ple

Sam

ple

Tim

eS

pati

al

Ind

ep.

Dep

end

ent

Sta

t.L

arg

eR

ejec

tR

ejec

tP

erio

dR

egio

nU

nit

Un

itV

ari

ab

leV

ari

ab

leT

est

Eff

ect

β=

0β

=10%

Inte

rper

son

al

con

flic

t(1

5)

An

der

son

etal.

2000a

1950–1997

US

Aan

nu

al

cou

ntr

yte

mp

vio

lent

crim

eY

YY

-A

ulici

ems

etal.

1995×

1992

Au

stra

lia

wee

km

un

icip

ali

tyte

mp

dom

esti

cvio

len

ceY

YY

-B

lakes

lee

etal.

2013

1971–2000

Ind

iaan

nu

al

mu

nic

ipality

rain

vio

lent

YY

Y-

&p

rop

erty

crim

eC

ard

etal.

2011†×

1995–2006

US

Ad

ay

mu

nic

ipality

tem

pd

om

esti

cvio

len

ceY

YY

-C

oh

net

al.

1997b

1987–1988

US

Ah

ou

rsm

un

icip

ality

tem

pvio

lent

crim

eY

YY

-Jaco

bet

al.

2007*×

1995–2001

US

Aw

eek

mu

nic

ipality

tem

pvio

lent

YY

Y-

&p

rop

erty

crim

eK

enri

cket

al.

1986‡

1985–1985

US

Ad

ay

site

tem

ph

ost

ilit

yY

YY

-L

arr

ick

etal.

2011*×†

1952–2009

US

Ad

ay

site

tem

pvio

lent

reta

liati

on

YY

Y-

Mare

s2013

1990–2009

US

Am

onth

mu

nic

ipality

tem

pvio

lent

crim

eY

YY

-M

igu

el2005×†

1992–2002

Tan

zan

iaan

nu

al

mu

nic

ipality

rain

mu

rder

YY

No

No

Meh

lum

etal.

2006

1835–1861

Ger

many

an

nu

al

pro

vin

cera

invio

lent

YY

Y-

&p

rop

erty

crim

eR

an

son

2012*×

1960–2009

US

Am

onth

cou

nty

tem

pp

erso

nal

vio

len

ceY

YY

-R

ott

on

etal.

2000b

1994–1995

US

Ah

ou

rsm

un

icip

ality

tem

pvio

lent

crim

eY

YY

-S

ekh

riet

al.

2013×

2002–2007

Ind

iaan

nu

al

mu

nic

ipality

rain

mu

rder

&Y

YY

-d

om

esti

cvio

len

ceV

rij

etal.

1994‡

1993–1993

Net

her

lan

ds

hou

rssi

tete

mp

police

use

of

forc

eY

YY

-

CHAPTER 4. CLIMATE AND CONFLICT 110T

able

4.1:

(con

tinued

)

Stu

dy

Sam

ple

Sam

ple

Tim

eS

pati

al

Ind

ep.

Dep

end

ent

Sta

t.L

arg

eR

ejec

tR

ejec

tP

erio

dR

egio

nU

nit

Un

itV

ari

ab

leV

ari

ab

leT

est

Eff

ect

β=

0β

=10%

Inte

rgro

up

con

flic

t(3

1)

Alm

eret

al.

2012

1985–2008

SS

Aan

nu

al

cou

ntr

yra

in/te

mp

civil

con

flic

tY

YN

oN

oA

nd

erso

net

al.

2013

1100–1800

Eu

rop

ed

ecad

em

un

icip

ality

tem

pm

inori

tyex

pu

lsio

nY

YY

-B

ai

etal.

2010

220–1839

Ch

ina

dec

ad

eco

untr

yra

intr

an

sbou

nd

ary

YY

Y-

Ber

gh

olt

etal.

2012+†

1980–2007

Glo

bal

an

nu

al

cou

ntr

yfl

ood

/st

orm

civil

con

flic

tY

No

No

YB

oh

lken

etal.

2011*+

1982–1995

Ind

iaan

nu

al

pro

vin

cera

inin

ter-

gro

up

YY

No

No

Bu

hau

g2010+

1979–2002

SS

Aan

nu

al

cou

ntr

yte

mp

civil

con

flic

tY

No

No

No

Bu

rke

2012*+†

1963–2001

Glo

bal

an

nu

al

cou

ntr

yra

in/te

mp

politi

cal

inst

ab

ilit

yY

YN

o�

No

Bu

rke

etal.

2009*+†c

1981–2002

SS

Aan

nu

al

cou

ntr

yte

mp

civil

con

flic

tY

YY

-C

ervel

lati

etal.

2011

1960–2005

Glo

bal

an

nu

al

cou

ntr

yd

rou

ght

civil

con

flic

tY

YY

-C

han

ey2011

641–1438

Egyp

tan

nu

al

cou

ntr

yN

ile

flood

sp

oliti

cal

inst

ab

ilit

yY

YY

-C

ou

tten

ier

etal.

2011+

1957–2005

SS

Aan

nu

al

cou

ntr

yP

DS

I�ci

vil

con

flic

tY

YY

-D

ell

etal.

2012+

1950–2003

Glo

bal

an

nu

al

cou

ntr

yte

mp

poli

tica

lin

stab

ilit

yY

YY

-&

civil

con

flic

tF

jeld

eet

al.

2012+†

1990–2008

SS

Aan

nu

al

pro

vin

cera

inin

ter-

gro

up

YY

No�

No

Hara

riet

al.

2013+

1960–2010

SS

Aan

nu

al

pix

el(1◦)

dro

ught

civil

con

flic

tY

YY

-H

end

rix

etal.

2012*+†

1991–2007

SS

Aan

nu

al

cou

ntr

yra

inin

ter-

gro

up

YY

Y-

Hid

alg

oet

al.

2010*+†

1988–2004

Bra

zil

an

nu

al

mu

nic

ipality

rain

inte

r-gro

up

YY

Y-

Hsi

an

get

al.

2011*+

1950–2004

Glo

bal

an

nu

al

worl

dE

NS

O⊕

civil

con

flic

tY

YY

-Jia

2012

1470–1900

Ch

ina

an

nu

al

pro

vin

ced

rou

ght/

flood

pea

sant

reb

ellion

YY

Y-

Ku

ng

etal.

2012

1651–1910

Ch

ina

an

nu

al

cou

nty

rain

pea

sant

reb

ellion

YY

Y-

Lee

etal.

2013

1400–1999

Eu

rop

ed

ecad

ere

gio

nN

AO⊗

vio

lent

con

flic

tY

YY

-L

evy

etal.

2005*+†

1975–2002

Glo

bal

an

nu

al

pix

el(2

.5◦)

rain

civil

con

flic

tY

YN

o�

No

Mayst

ad

tet

al.

2013+

1997–2009

Som

alia

month

pro

vin

cete

mp

civil

con

flic

tY

YY

-M

igu

elet

al.

2004+

d1979–1999

SS

Aan

nu

al

cou

ntr

yra

inci

vil

war

YY

Y-

O’L

au

gh

lin

etal.

2012*+†

1990–2009

E.

Afr

ica

month

pix

el(1◦)

rain

/te

mp

civil/in

ter-

gro

up

YY

Y-

Sale

hyan

etal.

2012

1979–2006

Glo

bal

an

nual

cou

ntr

yP

DS

I�ci

vil/in

ter-

gro

up

YY

Y-

Sars

on

s2011

1970–1995

Ind

iaan

nual

mu

nic

ipality

rain

inte

r-gro

up

YY

Y-

Th

eise

net

al.

2011+†

1960–2004

Afr

ica

annu

al

pix

el(0

.5◦)

rain

civil

con

flic

tY

No

No

No

Th

eise

n2012*+†

1989–2004

Ken

ya

an

nu

al

pix

el(0

.25◦)

rain

/te

mp

civil/in

ter-

gro

up

YY

No�

No

Tol

etal.

2009

1500–1900

Eu

rop

ed

ecad

ere

gio

nra

in/te

mp

tran

sbou

nd

ary

YY

Y-

Zh

an

get

al.

2007e

1400–1900

N.

Hem

.ce

ntu

ryre

gio

nte

mp

inst

ab

ilit

yY

YY

-

CHAPTER 4. CLIMATE AND CONFLICT 111T

able

4.1:

(con

tinued

)

Stu

dy

Sam

ple

Sam

ple

Tim

eS

pati

al

Ind

ep.

Dep

end

ent

Sta

t.L

arg

eR

ejec

tR

ejec

tP

erio

dR

egio

nU

nit

Un

itV

ari

ab

leV

ari

ab

leT

est

Eff

ect

β=

0β

=10%

Inst

itu

tion

al

bre

akd

ow

n&

pop

ula

tion

collap

se(1

5)

Bru

ckn

eret

al.

2011+

1980–2004

SS

Aan

nu

al

cou

ntr

yra

inin

st.

chan

ge

YY

Y-

Bu

ckle

yet

al.

2010**

1030–2008

Cam

bod

iad

ecad

eco

untr

yd

rou

ght

collap

seN

o-

--

Bu

ntg

enet

al.

2011**

400

BC

E–2000

Eu

rop

ed

ecad

ere

gio

nra

in/te

mp

inst

ab

ilit

yN

o-

--

Bu

rke

etal.

2010+†

1963–2007

Glo

bal

an

nu

al

cou

ntr

yra

in/te

mp

inst

.ch

ange

YY

Y-

Cu

llen

etal.

2000**

4000

BC

E–0

Syri

ace

ntu

ryco

untr

yd

rou

ght

collap

seN

o-

--

D’A

njo

uet

al

2012

550

BC

E–1950

Norw

ay

centu

rym

un

icip

ality

tem

pco

llap

seY

YY

-D

eMen

oca

l2001**

500–2000

Per

uce

ntu

ryco

untr

yd

rou

ght

coll

ap

seN

o-

--

Hau

get

al.

2003**

0–1900

Mex

ico

centu

ryco

untr

yd

rou

ght

collap

seN

o-

--

Kel

lyet

al.

2013

10050B

CE

–1950

US

Ace

ntu

ryst

ate

tem

p/ra

inco

llap

seY

YY

-K

enn

ett

etal.

2012

40

BC

E–2006

Bel

ize

dec

ad

eco

untr

yra

inco

llap

seN

o-

--

Ku

per

etal.

2006

8000–2000

BC

EN

.A

fric

am

ille

nia

regio

nra

inco

llap

seN

o-

--

Patt

erso

net

al.

2010

200

BC

E–1700

Icel

an

dd

ecad

eco

untr

yte

mp

collap

seN

o-

--

Sta

hle

etal.

1998

1200–2000

US

Am

ult

iyea

rm

un

icip

ality

PD

SI�

collap

seN

o-

--

Yan

chev

aet

al.

2007**

2100

BC

E–1700

Ch

ina

centu

ryco

untr

yra

in/te

mp

collap

seN

o-

--

Zh

an

get

al.

2006

1000–1911

Ch

ina

dec

ad

eco

untr

yte

mp

civil

con

flic

tY

YY

-&

collap

se

Numberofstudies(6

0to

tal):

50

47

37

1Fractionusing

statisticalte

sts:

100%

94%

74%

2%

“Sta

t.T

est”

isY

ifth

eanaly

sis

use

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rmal

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stic

al

met

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fluen

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ate

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able

sand

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oth

esis

test

ing

pro

cedure

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arg

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poin

tes

tim

ate

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the

effec

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consi

der

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bst

anti

al

by

the

auth

ors

or

isgre

ate

rin

magnit

ude

than

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the

mea

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imate

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able

s.“R

ejec

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=0”

isY

ifth

est

udy

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cts

an

effec

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zeof

zero

at

the

95%

confiden

cele

vel

.�

the

effec

tsi

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the

study

isst

ati

stic

ally

signifi

cant

at

the

10%

level

but

not

at

the

5%

level

.“R

ejec

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=10%

”is

Yif

the

study

isable

tore

ject

the

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esis

that

the

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larg

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the

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incl

imate

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able

s.*

Show

nin

Fig

.2.

**

Show

nin

Fig

.3.×

Show

nin

Fig

.4.

+Show

nin

Fig

.5.†

Rea

naly

zed

usi

ng

the

com

mon

stati

stic

al

model

conta

inin

glo

cati

on

fixed

effec

tsand

tren

ds

(see

Supple

men

tary

Info

rmati

on).

‡A

ctual

exp

erim

ent.

aA

lso

see

ref

(Ander

son,

Bush

man,

and

Gro

om

,1997).

bA

lso

see

dis

cuss

ion

inre

f(B

ush

man,

Wang,

and

Ander

son,

2005).

cSSA

isSub-S

ahara

nA

fric

a.

Als

ose

edis

cuss

ion

inre

fs(S

utt

on

etal.,

2010;

Buhaug,

Heg

re,

and

Str

and,

2010;

Buhaug,

2010a,b

;B

urk

eet

al.,

2010c,

a,b

).d

Als

ose

edis

cuss

ion

inre

f(C

icco

ne,

2011b;

Mig

uel

and

Saty

anath

,2011).

eA

lso

see

ref

(Zhang

etal.,

2011).�

PD

SI

isth

eP

alm

erD

rought

Sev

erit

yIn

dex

.⊕

EN

SO

isth

eE

lN

ino-S

outh

ern

Osc

illa

tion.⊗

NA

Ois

the

Nort

hA

tlanti

cO

scilla

tion.

112

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Appendix A

Adaptation to climate appendix

A.1 Understanding changes in climate and

agriculture over time

Figure A.1 plots changes in GDD 0-29C and GDD >29C between 1980-2000 for our samplecounties. The left plot shows that while increases in “beneficial” and “harmful” GDD arepositively correlated, many counties experienced increases in one and decreases in theother. The right panel plots the relationship between change in log corn yields and changein harmful GDD >29C over the same period. Because both figures show large outliers interms of either temperature or log yields (the ∼ 10 points plotted as white circles in thefigure), and we run regressions with and without these outliers to make sure they are notdriving our results. Figure A.2 maps these changes in GDD, showing that extreme-heatoutliers are clustered among a few counties in southern Texas.

There are two potential concerns with the variation in temperature we are using in thelong differences. The first is that state fixed effects could absorb most of the meaningfulvariation in temperature changes over time, and the second is that the apparent long-runchanges in temperature might just reflect short-run variation around endpoint years - e.g.single hot or cold years that create large differences between endpoints but do not reflectunderlying long-term changes in temperature. If this latter concern were true, then thepanel and long difference approaches will mechanically deliver estimates of yield responsesthat are similar to each other (albeit with the LD being much noisier), which in turn wouldlead us to erroneously conclude that there had been “no adaption” when in fact there wasno underlying trend to adapt to.

To address these concerns, we begin by more carefully characterizing the variation inextreme heat in the long differences and the panel, and comparing this variation to theprojected future changes in extreme heat. Table A.1 shows the amount of variation leftin our extreme heat variable after accounting for the other climate variables and various

APPENDIX A. ADAPTATION TO CLIMATE APPENDIX 134

Figure A.1: Changes in GDD and corn yield for corn-growing counties eastof the 100th meridian

.

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ange

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DD 0

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Left panel: changes in GDD 0-29C and GDD>29C over the 1980-2000 period. Middlepanel: change in log corn yields and GDD>29C over the same period. Right panel: changesin GDD>29C, 1955-75 versus 1980-2000. To check robustness we run the long differencesregressions with and without the points shown as white circles.

sets of fixed effects, in both the panel and the long differences. The variation in long-runchanges in extreme heat is smaller than the inter-annual variation in extreme heat, but theother climate controls and fixed effects absorb a smaller percentage of the variation in thelong differences (as shown by the 3rd and 4th columns in the table) than in the panel.

Figure A.3 relates the distribution of observed changes in GDD>29 to the extent ofvariation in projected changes in GDD>29, plotting the raw distributions (left panel)and the residualized distributions (right panel). The conditional distribution of futurechanges is calculated for each of the 18 climate models as the residuals from a regression ofGDD>29C on GDD0-29C and a piecewise function of precipitation (i.e. the other climatevariables in all of our regressions). Given our empirical approach, we are most interested inthe overlap in the conditional distributions, and the Figure demonstrates the substantialoverlap between the variation we are exploiting in the long differences, the variation weexploit in the panel, and the variation we use in the projections (after accounting forprojected changes in the other climate variables). This gives us additional confidence thatour projections are not wild extrapolations from historical experience.

To address concerns that the “changes” in temperature we observe over time are in-deed meaningful and not a function of short-run variation around endpoint years, we firstestimate the trend in temperature and precipitation from 1978-2002 for each county in our


Figure A.2: Map of changes in GDD 0-29C and GDD above 29C between1980-2000.

GDD 0−29C

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change in GDD >29C

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change in GDD >29C

−40 −20 0 20 40

Shown are corn-growing counties east of the 100th meridian. Rightmost panel re-plots thechange in GDD >29 dropping the outliers indicated in Figure A.1.

main sample by running the regression

ln(climt) = α+ βt+ εt, (A.1)

where t is the sample year. Results for our main GDD>29C variable are shown in FigureA.4 for the main corn belt states. Plots represent the distribution of annual percentagechanges in GDD>29C across counties within a given state (i.e. the kernel density of βsestimated in Equation (A.1)), and show that annual changes in extreme heat vary by 2-4percentage points within states. This represents substantial variation over our 20 yearestimation period. For instance, estimates for Iowa suggest that changes over 20 yearsranged from 80% declines in exposure to extreme heat to slight increases in exposure;estimates for Illinois range from 40% decreases to 70% increases.

Second, we show in a simulation that the observed distribution of temperature changesover our study period is highly unlikely to be generated by a time series with a fixed mean.For each county in our data, we calculate the observed mean µi and standard deviation σi ofGDD>29C between 1978-2002, and then use these parameters to generate 1000 simulatedpanel datasets, where the observation for GDD > 29it is a draw from a normal distribution


Figure A.3: Distributions of GDD > 29 for the 1980-2000 period (red lines)and as projected for 2050 across 18 climate models for the A1B scenario(blue lines).

−50 0 50 100 150

0.00

0.02

0.04

0.06

0.08

0.10

GDD > 29C

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sity

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sity

LD: state FE

LD: no FE

Panel: county FE, year FE

Panel: county FE, state-year FE

Panel: county FE, year FE, state trends

Panel: no FEConditional

futureprojectionsRaw future projections

Raw LD

Raw Panel

Left panel: raw changes. Right panel: changes conditional on other climate variables(GDD0-29C, precipitation) and on various sets of fixed effects as indicated. Distributionsare area weighted, as in our main regressions.

∼ N(µi, σi). For each of these simulated panels we then compute long differences for eachcounty (differencing the 5-year averages at the endpoints each county’s time series, asin our main exercise). These long differences are therefore generated from data with no“permanent” change in temperature, with variation in the LD by construction coming onlyfrom random variation in temperature around the endpoints. We can then compare thedistribution of these simulated changes to our actual observed distribution of ∆GDD>29to understand whether the changes we observed were likely generated from data with no“permanent” change in temperature.

The results are shown in Figure A.5, with the observed distributions of ∆GDD>29shown in red and the 1000 simulated distributions shown in grey (the right panel is for1980-2000, the left panel repeats the exercise for 1955-1975 with corresponding data). Thisexercise suggests the observed changes over time are extremely unlikely to be generatedfrom data with a fixed mean. The distribution of observed changes over 1955-1975, a periodof substantial cooling in the central US, is far to the left of all of the simulated distributionsfor that period; the observed distribution in 1980-2000, a period of substantial averagewarming across the US, is shifted substantially to the right of the simulated distributions


for that period.As a third test for whether our observed temperature changes were “permanent”, we

check for mean reversion. Even if there are “real” temperature changes during a givendecade, the longer-term mean might not change if a period of warming was then followedby a period of cooling. If farmers know about this cyclicality in temperature, it thereforemight make sense to not adapt to a temperature increase. To test for mean reversion intemperature we compare our ∆GDD>29 over the main 1980-2000 period with changes inthe previous 1955-1975 period (with 5-year averaging at endpoints, we are then using twonon-overlapping but contiguous periods from 1953-1977 and from 1978-2002). The dataare shown in the right panel of updated Figure A1, and estimating the following regression:

∆GDD1980−2000is = α+ βGDD1955−1975

is + ηs + εis (A.2)

(where i is county and s indicates state) gives an estimate of β which is positive but small(β = 0.10) and statistically insignificant with state-level clustering. This is inconsistentwith a mean reversion story: although many areas did cool during 1955-1975, these werenot on average the areas that differentially warmed over the subsequent 20 years. Thissuggests that, based on the historical record, farmers would have no reason to believe the1980-2000 changes were impermanent.

Finally, we note that the scientific literature provides very strong evidence that futuretemperatures across the US are going to continue to increase for centuries – a conclusionthat was already understood and publicized by the 1980s, and solidified with the releaseof the IPCC’s First Assessment Report in 1990. This report concluded that mean tem-peratures were likely to increase by 0.3C/decade over the next century, with land areasheating up faster than oceans. To the extent that farmers were aware of what scientistswere saying (and other papers in this literature, e.g. Kelly, Kolstad and Mitchell (2005),assume that they were), this again suggests that farmers who experienced warming during1980-2000 would have no reason to believe that these changes were impermanent.

A.2 Correlates of trends in extreme heat

Tables A.2 and A.3 investigate the sensitivity of our main long difference results to control-ling for county characteristics. Table A.2 shows that changes from 1980-2000 in GDD>29are not strongly correlated with baseline measures of population density, various measuresof farm land use, and characteristics of the soil. Table A.3 shows regression coefficientswhen controlling for these variables. Adding controls does not substantially change ourresults.


Figure A.4: Distribution of estimated annual growth in GDD > 29 forcounties in 13 corn belt states.

010

2030

40

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

All States0

2040

6080

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

Iowa

010

2030

4050

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

Illinois

020

4060

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

Indiana

2030

4050

60

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

Kansas

010

2030

4050

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

Kentucky

510

1520

25

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

Michigan

010

2030

40

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

Minnesota

020

4060

80

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

Missouri

1020

3040

5060

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

Nebraska

020

4060

80

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

NorthDakota

010

2030

40

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

Ohio

1020

3040

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

SouthDakota

010

2030

-.08 -.06 -.04 -.02 0 .02 .04 .06 .08

Wisconsin

Horizontal axis for each plot is the estimated annual growth (% per year) in GDD > 29for 1978-2002. Vertical axis is kernel density.

A.3 Robustness to outliers

Robustness of our corn yield results to dropping outliers is explored in Table A.4. Pointestimates decline slightly when outliers are dropped – not surprising given that nearly allof the outliers experienced both yield declines and large increases in exposure to extremeheat – but coefficients are statistically indistinguishable from estimates on the full sample.

Robustness of the results on alternate adaptation margins to dropping outliers is shownin Table A.5. Here dropping the 5 extreme heat outliers (0.003% of the sample) does havea substantial effect on farm area, on the number of farms, and on farm land values. When


Table A.1: Yield response to GDD>29 across different panel and long differencemodels, and variation in GDD>29 after accounting for fixed effects and other climatecontrols in these models.

DV: log yield DV: GDD>29

β se R2 σ share>5 share>10

PanelNone -0.0036 0.0005 0.00 62.83 0.53 0.50Climate -0.0057 0.0010 0.70 33.11 0.42 0.35Climate, state FE -0.0067 0.0009 0.80 27.10 0.34 0.26Climate, county FE, year FE -0.0056 0.0007 0.91 20.79 0.32 0.21Climate, county FE, state trends -0.0055 0.0007 0.91 20.66 0.32 0.21Climate, county FE, state-year FE -0.0062 0.0007 0.97 9.78 0.22 0.10

Long DifferencesNone -0.0077 0.0017 0.00 9.44 0.31 0.14Climate -0.0053 0.0010 0.34 8.23 0.27 0.12Climate, state FE -0.0044 0.0008 0.60 6.63 0.17 0.05

The first two columns display the estimated effect of GDD > 29 on log of corn yield and itsstandard error, estimated using alternate versions of Equation (2.10) or its panel analog; allestimates are statistically significant at the 1% level. Remaining columns pertain to regressions ofGDD > 29 on GDD<29, a piecewise linear function of precipitation, and the listed fixed effects,and show the R2 of that regression, the standard deviation of the GDD>29 residuals, and thepercentage of those residuals larger than 5C or 10C. Panel regressions are based on 48,465county-year observations, and long difference regressions based on 1,531 county observations.

these outliers are dropped, extreme heat coefficients on these variables drops by at least60-70% and becomes statistically insignificant. For the reason we focus on the results forthe trimmed sample in the main text.

A.4 Choice of time period

Our main specification focuses on changes in climate and yields of the 1980-2000 period.We focus on this period for a few reasons. First, relative to earlier periods, and as shownin Figure A.7, global warming had begun in earnest over this period, and counties hadexperienced on average much more warming. Importantly, many more counties had expe-rienced at least 1C warming over the period, making this period more representative ofthe warming that climate models predict will occur over the next few decades and thus abetter baseline with which to project future impacts. Second, prior to 1980, scientific opin-ion was relatively split as to whether the future climate would be cooler or warmer than


Figure A.5: Observed versus simulated changes in GDD>29

The observed distribution of changes in GDD>29 (in red), compared to 1000 distributionsgenerated from data with the same variance but no change in mean (shown in grey). Theleft panel is real and simulated changes between 1955-1975, the right panel for 1980-2000.

the current climate, and in fact there was significant concern about “global cooling” (e.g.Gwynne (1975)). Growing scientific and public recognition of “global warming” during the1980’s and 1990’s – i.e. a recognition that increasing greenhouse gas emissions would leadto future warming – again makes this period more relevant for projecting future impactsbecause there was recognition that the climate was warming and would continue to warm.

Nevertheless, Figure 2.4 directly compares our benchmark 1980-2000 estimate to esti-mates using alternate time periods and differencing lengths, and shows that these alternateestimates are largely indistinguishable from our main estimate. Figure A.6 displays pointestimates and their confidence intervals from each of these regressions (rather than com-parisons with the 1980-2000 estimate); all of these estimates are negative, and in only 8out of 39 cases do we fail to reject no effect of extreme heat on corn yields.

As a final robustness test on our choice of time period, we vary the length of theendpoints over which our two periods are averaged. We begin with our 1980-2000 period,and average our endpoints over ten years instead of five – i.e. the long difference is now1995-2005 average minus 1975-1985 average. We include in the sample any counties thatreported growing corn in at least one year in both periods, or restrict the sample to countiesthat grew corn in all years in both averaging periods. Results are given in Columns 1 and 2of Table A.6. Coefficients on extreme heat in both specifications are slightly more negativethan our baseline estimates and highly significant.

Finally, we utilize our full 1950-2005 sample, split it into 28-year periods (1950-1977


Table A.2: Coefficients and p-values of univariate regressions of county characteristicson change in extreme heat exposure

Coefficient p-ValuePop density 1980 1.96 0.16

Farm area 1978 889.29 0.14

Corn area 1980 273.31 0.31

County area 0.67 0.56

Irrigated area 1982 338.62 0.15

Farm value 1978 16.49 0.15

Percent of soil that is clay -0.04 0.49

Water capacity of soil -0.01 0.60

Percent of soil that is high quality 0.13 0.20

Income per capita 1978 7.59 0.70

Table displays coefficients and p-values from regressions of each county characteristic on change inGDD> 29 from 1980-2000 and state fixed effects. Standard errors for each regression are clusteredat the state level.

and 1978-2005), average both climate and crop yields within each period, difference theseaverages, and then run our basic long differences specification on these two time periods.This is equivalent to smoothing our data with a 28-year running mean, and then differenc-ing between the years 1991 and 1964. We similarly restrict the sample to include eitherall counties reporting growing corn in at least one year in both periods (column 3), orsuccessively limit the sample to counties with at least 40, 50, or 56 observations (columns4-6).

The coefficient on GDD above 29C is again large, negative, and highly significantacross all specifications. Point estimates are in fact substantially more negative than forour baseline 1980-2000 period. One explanation for this is that farmers have become lesssensitive to temperature over time, with our main 1980-2000 specification focusing on alater (and thus less sensitive) period. But both Figure 2.4 and Figure A.8 (see discussionbelow) show that there is little evidence that temperature sensitivities have declined overtime. We can also run the panel model for the full 1950-2005 period (shown in column 7of Table A.6), and we find that the panel coefficient on extreme heat is somewhat morenegative that for the 1980-2000 period but not substantially so. An alternate explanation isthat if measurement error in temperature is uncorrelated across years, then averaging overmore years will reduce attenuation bias, resulting in larger (in absolute value) coefficients.


Table A.3: Robustness of long difference results to addition of county control vari-ables

(1) (2)GDD below threshold 0.0000 0.0003∗

(0.0003) (0.0001)

GDD above threshold -0.0046∗∗∗ -0.0043∗∗∗

(0.0010) (0.0008)

Precip below threshold 0.0429∗∗∗ 0.0300∗∗∗

(0.0154) (0.0104)

Precip above threshold 0.0022 0.0028∗∗∗

(0.0015) (0.0009)Observations 1525 1525R squared 0.387 0.637Fixed Effects None StateControls Yes Yes

Table displays long difference regression results from 1980-2000. Standard errors for eachregression are clustered at the state level. Temperature threshold is 29◦C and precipitationthreshold is 42 cm. Control variables are population density in 1980, total farm area in 1978, totalcorn area in 1980, total county area, irrigated area in 1982, average farm value in 1978, percent ofsoil that is clay, water capacity of soil, percent of soil that is high quality, and income per capitain 1978. Column 2 also includes state fixed effects. Asterisks indicate statistical significance at the1% ∗∗∗,5% ∗∗, and 10% ∗ levels.

While this explanation is hard to either support or rule out with the data, it appears moreplausible than declining sensitivities.

Nevertheless, we cannot reject that the long differences estimates for the full periodare the same than the panel estimates over the same period, and so these results do notsuggest a qualitative or quantitatively different conclusion from that which we draw fromour baseline specification. We view these results as yet more evidence that farmers havebeen unable to adapt very effectively in the long run, and these results suggest that ourbaseline estimates are somewhat conservative in terms of levels effects of extreme heat onyields..

We conduct analogous exercise for our panel results, to ensure that our panel estimatesare also not being driven by our choice of time period. Since our data span five decades, weestimate our main panel regressions for each decade from the 1950’s to the 1990’s (resultsfrom running the panel on the full dataset are given in the last column in Table A.6). InFigure A.8 we show the coefficient on GDD above 28C and its 95% confidence interval foreach of these five regressions. The estimates vary only slightly between decades and thereis no clear pattern suggesting that corn yields have become less sensitive to short-termdeviations in weather over time.


Table A.4: Robustness of corn yield results to dropping outliers

(1) (2) (3) (4)full trimmed full trimmed

GDD below threshold 0.0002 0.0002 0.0003∗ 0.0002(0.0002) (0.0002) (0.0002) (0.0001)

GDD above threshold -0.0044∗∗∗ -0.0043∗∗∗ -0.0037∗∗∗ -0.0032∗∗∗

(0.0008) (0.0009) (0.0009) (0.0009)

Precip below threshold 0.0297∗∗ 0.0309∗∗ 0.0115∗∗ 0.0117∗∗

(0.0125) (0.0130) (0.0046) (0.0045)

Precip above threshold 0.0034∗∗∗ 0.0034∗∗∗ 0.0029∗∗∗ 0.0030∗∗∗

(0.0008) (0.0008) (0.0007) (0.0007)

Constant 0.2397∗∗∗ 0.2403∗∗∗ 0.2400∗∗∗ 0.2409∗∗∗

(0.0124) (0.0125) (0.0115) (0.0118)Observations 1531 1521 1531 1521R squared 0.610 0.624 0.602 0.617Fixed Effects State State State StateT threshold 29 29 28 28P threshold 42 42 50 50

All regressions use log of corn yields as the dependent variable, and use temperature andprecipitation thresholds as indicated at the bottom of the table. Columns 1 and 3 are on the fullsample, columns 2 and 4 drop the outliers indicated in Figure A.1. Standard errors are clusteredat the state level. Asterisks indicate statistical significance at the 1% ∗∗∗,5% ∗∗, and 10% ∗ levels.

While this unchanging sensitivity of yield to extreme heat over time could be interpretedas additional evidence of a lack of adaptation (as in Schlenker and Roberts (2009a)), wenote that whether responses to short-run variation have changed over time is conceptuallydistinct from whether farmers have responded to long-run changes in average temperature.In particular, there is no reason to expect farmers to respond similarly to these two dif-ferent types of variation. Indeed, farmers could adapt completely to long-run changes intemperature such that average yields do not change – e.g. by adopting a new variety thaton average performs just as well in the new expected temperature as the old variety didunder the old average temperature – but still face year-to-year variation in yield due torandom deviations in temperature about its new long-run average. As such, we view thisexercise more as a test of the robustness of the panel model than as evidence of (a lack of)adaptation per se.


Tab

leA

.5:

Rob

ust

nes

sof

resu

lts

onal

tern

ate

adap

tati

ons

tore

mov

alof

outl

iers

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Cor

nar

eaC

orn

area

Corn

%C

orn

%F

arm

are

aF

arm

are

a#

farm

#fa

rmG

DD

bel

owth

resh

old

0.00

130.

0010

0.0

003∗∗∗

0.0

003∗∗∗

-0.0

000

-0.0

001

-0.0

001

-0.0

002

(0.0

012)

(0.0

012)

(0.0

001)

(0.0

001)

(0.0

001)

(0.0

001)

(0.0

003)

(0.0

002)

GD

Dab

ove

thre

shol

d-0

.003

8-0

.000

5-0

.0007∗∗

-0.0

009∗∗

-0.0

010∗∗

0.0

000

-0.0

023∗

-0.0

007

(0.0

048)

(0.0

038)

(0.0

003)

(0.0

004)

(0.0

004)

(0.0

004)

(0.0

011)

(0.0

010)

Pre

cip

bel

owth

resh

old

0.04

040.

0264

-0.0

006

-0.0

004

0.0

067

0.0

037

0.0

077∗∗

0.0

021

(0.0

485)

(0.0

637)

(0.0

030)

(0.0

034)

(0.0

043)

(0.0

035)

(0.0

036)

(0.0

029)

Pre

cip

abov

eth

resh

old

-0.0

079

-0.0

051

-0.0

015

-0.0

016

-0.0

001

0.0

007

-0.0

023

-0.0

013

(0.0

067)

(0.0

063)

(0.0

010)

(0.0

010)

(0.0

008)

(0.0

007)

(0.0

032)

(0.0

033)

Con

stan

t-0

.027

3-0

.013

0-0

.0164∗∗∗

-0.0

174∗∗∗

-0.0

649∗∗∗

-0.0

614∗∗∗

-0.1

881∗∗∗

-0.1

836∗∗∗

(0.0

661)

(0.0

687)

(0.0

045)

(0.0

045)

(0.0

079)

(0.0

075)

(0.0

156)

(0.0

157)

Ob

serv

atio

ns

1516

1511

1521

1516

1528

1523

1531

1526

Mea

nof

Dep

Var

iable

0.07

30.

075

0.0

02

0.0

02

-0.0

69

-0.0

68

-0.2

02

-0.2

02

Rsq

uar

ed0.

642

0.64

50.4

18

0.4

18

0.3

87

0.3

99

0.4

78

0.4

88

Fix

edE

ffec

tsS

tate

Sta

teS

tate

Sta

teS

tate

Sta

teS

tate

Sta

teT

thre

shol

d29

2929

29

29

29

29

29

Pth

resh

old

4242

42

42

42

42

42

42

Dep

end

ent

vari

able

isd

iffer

ence

inlo

gof

corn

acre

s(C

olu

mn

s1-2

),d

iffer

ence

insh

are

of

agri

cult

ura

lare

ap

lante

dto

corn

(Col

um

ns

3-4)

,d

iffer

ence

into

tal

log

farm

area

(Colu

mn

s5-6

),an

dd

iffer

ence

inlo

gnu

mb

erof

farm

ers

(Colu

mn

s7-8

).A

llre

gres

sion

sar

elo

ng

diff

eren

ces

from

1980

-200

0,an

dev

ennu

mb

ered

regre

ssio

ns

hav

eth

esa

mp

letr

imm

edof

ou

tlie

rsin

dic

ate

din

Fig

ure

A.1

.A

llre

gres

sion

sar

ew

eigh

ted

by

aver

age

agri

cult

ura

lare

afr

om

1978-2

002.

Sta

nd

ard

erro

rsare

clu

ster

edat

the

state

leve

l.A

ster

isks

ind

icat

est

atis

tica

lsi

gnifi

can

ceat

the

1%∗∗∗ ,

5%∗∗

,an

d10%∗

leve

ls..


Tab

leA

.6:

Lon

gdiff

eren

ces

regr

essi

ons

wit

hen

dp

oints

aver

aged

over

longe

rp

erio

ds.

(1)

(2)

(3)

(4)

(5)

(6)

(7)

1980

-200

019

80-2

000

1950-2

005

1950-2

005

1950-2

005

1950-2

005

pan

el50-0

5G

DD

bel

ow0.

0000

0.00

000.0

008∗∗

0.0

008∗∗

0.0

009∗∗

0.0

010∗∗

0.0

004∗∗∗

(0.0

002)

(0.0

002)

(0.0

003)

(0.0

003)

(0.0

003)

(0.0

003)

(0.0

001)

GD

Dab

ove

-0.0

050∗∗∗

-0.0

047∗∗∗

-0.0

090∗∗∗

-0.0

091∗∗∗

-0.0

102∗∗∗

-0.0

096∗∗

-0.0

065∗∗∗

(0.0

010)

(0.0

011)

(0.0

025)

(0.0

027)

(0.0

030)

(0.0

034)

(0.0

006)

Pre

cip

bel

ow0.

0234∗∗∗

0.02

45∗∗∗

0.0

480∗∗∗

0.0

460∗∗∗

0.0

457∗∗∗

0.0

450∗∗∗

0.0

172∗∗∗

(0.0

045)

(0.0

045)

(0.0

047)

(0.0

049)

(0.0

049)

(0.0

046)

(0.0

022)

Pre

cip

abov

e0.

0026

0.00

270.0

021

0.0

023

0.0

022

0.0

020

-0.0

020∗∗∗

(0.0

019)

(0.0

019)

(0.0

033)

(0.0

035)

(0.0

036)

(0.0

039)

(0.0

003)

Con

stan

t0.

2805∗∗∗

0.28

09∗∗∗

0.5

206∗∗∗

0.5

232∗∗∗

0.5

237∗∗∗

0.5

117∗∗∗

2.7

418∗∗∗

(0.0

074)

(0.0

080)

(0.0

101)

(0.0

110)

(0.0

123)

(0.0

132)

(0.2

234)

Ob

serv

atio

ns

1950

1451

2241

1711

1262

956

107290

Mea

nof

Dep

Var

.e0.

310.

310.5

70.5

70.5

80.5

74.4

2R

squ

ared

0.62

70.

670

0.6

87

0.7

19

0.7

22

0.7

34

0.8

21

Per

iod

1ye

ars

1975

-198

519

75-1

985

1950-1

977

1950-1

977

1950-1

977

1950-1

977

Per

iod

2ye

ars

1995

-200

519

95-2

005

1978-2

005

1978-2

005

1978-2

005

1978-2

005

Min

.yrs

insa

mp

le2

All

240

50

All

Any

All

regr

essi

ons

use

log

ofco

rnyie

lds

asth

ed

epen

den

tva

riab

le,

an

du

seth

e29C

tem

per

atu

rean

d42cm

pre

cip

itati

on

thre

shold

s.T

he

sam

ple

per

iod

isei

ther

1975

-200

5(c

olu

mn

s1-

2)or

1950-2

005

(colu

mn

s3-7

),w

ith

end

poin

tsav

eraged

over

the

two

diff

eren

tp

erio

ds

given

inth

eb

otto

mof

the

tab

le.

As

ind

icat

edin

the

last

lin

eof

the

tab

le,

sam

ple

sei

ther

incl

ud

eco

unti

esth

at

rep

ort

at

leas

ton

eye

arof

grow

ing

corn

inb

oth

per

iod

s(c

olu

mn

san

d3),

counti

esth

at

gre

wco

rnin

all

years

inth

esa

mp

le(c

olu

mn

s2

and

6),

orco

unti

esth

atgr

ewco

rnin

atle

ast

40or

50yea

rsof

the

56-y

ear

sam

ple

(colu

mn

s4

an

d5).

Th

efi

nal

mod

el(c

olu

mn

7)is

ap

anel

mod

elov

erth

efu

ll19

50-2

005

per

iod

.S

tan

dard

erro

rsare

clu

ster

edat

the

state

level

,an

dast

eris

ks

indic

ate

stat

isti

cal

sign

ifica

nce

atth

e1%

∗∗∗ ,

5%∗∗

,an

d10

%∗

leve

ls.


Figure A.6: Long difference estimates under various starting years anddifferencing lengths.

-.015

-.01

-.005

0.0

05C

oeffi

cien

t of G

DD A

bove

Thr

esho

ld

1950 1960 1970 1980 1990 2000Starting Year

5 Year Differences

-.015

-.01

-.005

0.0

05C

oeffi

cien

t of G

DD A

bove

Thr

esho

ld

1950 1960 1970 1980 1990Starting Year

10 Year Differences

-.015

-.01

-.005

0.0

05C

oeffi

cien

t of G

DD A

bove

Thr

esho

ld

1950 1960 1970 1980 1990Starting Year

15 Year Differences

-.015

-.01

-.005

0.0

05C

oeffi

cien

t of G

DD A

bove

Thr

esho

ld

1955 1960 1965 1970 1975 1980Starting Year

20 Year Differences

-.015

-.01

-.005

0.0

05C

oeffi

cien

t of G

DD A

bove

Thr

esho

ld

1955 1960 1965 1970 1975Starting Year

25 Year Differences

-.015

-.01

-.005

0.0

05C

oeffi

cien

t of G

DD A

bove

Thr

esho

ld

1955 1960 1965 1970Starting Year

30 Year Differences

Dots are point estimates and whiskers are 95% confidence intervals.

A.5 Measurement error

As discussed in the main text, one concern is that fixed effects estimators are more likelythan long differences estimates to suffer attenuation bias if climate variables are measuredwith error. Following Griliches and Hausman (1986), we compare fixed effectsand first dif-ference estimates with random effects estimates, with the expectation that if measurementerror in our climate variables is a problem, then estimates from a random effects estimationshould be larger in absolute value than the fixed effects estimates which in turn should belarger than estimates using first differences.

Table A.7 presents the results of a horse race between these three estimators. The first


Figure A.7: Distribution of the change in average growing season temper-ature across our sample counties, for the period 1960-1980 (dotted line)or the period 1980-2000 (solid line).

−1.0 −0.5 0.0 0.5 1.0 1.5

0.0

0.2

0.4

0.6

0.8

1.0

1.2

1.4

Change in Temperature (C)

Den

sity

1960−1980

1980−2000

column presents unweighted fixed effects estimates. The random effects estimates in Col-umn 2 are remarkably similar to the fixed effects estimates. The main coefficient of interestfor GDD above 28◦ is smaller in absolute value by a modest 7%. Column 3 shows that thefirst difference estimator also produces a very similar effect of increases in temperaturesabove 28◦ on yields. Results suggest that measurement error is not responsible for the lackof difference between fixed effects estimators and long differences that we observe in thedata.

Functional Form

Our use of growing degree days to capture nonlinearities is primarily motivated by resultsfrom the agronomy literature suggesting that plant growth increases linearly with temper-ature up to a certain threshold level, and then declines with further temperature increases.Figure 2.3 in the main text shows that our results produce this relationship. Our piecewiselinear approximation will be misspecified in the presence of strong nonlinearities withinthe ranges from 0-29 and 29 and above. Schlenker and Roberts (2009a) show that thepiecewise linear relationship achieved with growing degree days estimates that use either


Figure A.8: Panel estimates of the effect of extreme heat on log corn yieldsby decade.

0-.0

02-.0

04-.0

06-.0

08C

oeffi

cien

t of G

DD A

bove

Thr

esho

ld

1950-59 1960-69 1970-79 1980-89 1990-99Decade

Figure shows point estimate and 95% confidence interval for regressions run separatelyfor each decade. The black line is the coefficient on extreme heat from our baseline panelregression (Column 3 in Table 2.1) . All regressions include county and time fixed effectsand are weighted by average corn area in the county during the relevant decade, with errorsclustered at the state level.

a higher order polynomial or a set of temperature bins measuring the days of exposure tovarious temperature ranges. These results strongly suggest that use of growing degree daysis not affected by misspecification due to nonlinearity.

Nevertheless, we re-estimate both our main panel and long difference specificationsusing three degree bins. In both models we include the same functions of precipitation aswere included in the main specifications. Figure A.9 shows the results. Both the paneland long difference specifications using temperature bins produce similar results to thoseusing growing degree days, consistent with Schlenker and Roberts (2009a). Our use ofgrowing degree days does not seem to misrepresent the relationship between temperature


Table A.7: Understanding measurement error through the comparison of panel esti-mators

(1) (2) (3)Fixed Effects Random Effects First Difference

GDD below threshold 0.0004∗∗∗ 0.0003∗∗∗ 0.0003∗∗∗

(0.0001) (0.0001) (0.0001)

GDD above threshold -0.0045∗∗∗ -0.0042∗∗∗ -0.0045∗∗∗

(0.0005) (0.0005) (0.0004)

Precip below threshold 0.0045∗∗ 0.0040∗∗ 0.0054∗∗∗

(0.0018) (0.0017) (0.0018)

Precip above threshold -0.0011∗ -0.0011 -0.0009(0.0006) (0.0007) (0.0006)

Constant 3.2154∗∗∗ 3.6483∗∗∗ 0.0703∗∗

(0.2877) (0.1648) (0.0343)Observations 48465 48465 45405R squared 0.463 0.494Fixed Effects Cty, Yr Yr YrT threshold 28 28 28P threshold 50 50 50

All regressions use log of corn yields as the dependent variable. All regressions are unweighted.Standard errors are clustered at the state level. Asterisks indicate statistical significance at the1% ∗∗∗,5% ∗∗, and 10% ∗ levels.

and yields.

A.6 Effects on soy productivity

Estimates of the impact of extreme heat on (log) soy yields are shown in Figure A.10. Thehorizontal line in each panel is the 1978-2002 panel estimate of β2 for soy which is -0.0047.The thresholds for temperature and precipitation are 29◦ and 50 cm, which are those thatproduce the best fit for the panel model. The average response to extreme heat across the39 estimates is -0.0032, giving a point estimate of longer run adaptation to extreme heat ofabout 30%. This estimate is slightly larger but of similar magnitude to the corn estimate,and we are again unable to reject that the long differences estimates are different than thepanel estimates. As for corn, we conclude that there is limited evidence for substantialadaptation of soy productivity to extreme heat.


Figure A.9: Relationship between corn yields and temperature.

-.08

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Estimates represent the change in log corn yield under an additional day of exposure toa given ◦C temperature, relative to a day spent at 0-3◦C. Estimates of 3◦C temperaturebins are used for long difference and panel versions of binned regressions. Dots representmidpoints of bins. GDD regressions are identical to those in Figure 2.3 of the main text.The shaded area is the confidence interval of the long difference estimates where temperatureis measured with GDD.

A.7 Revenues and profits

A basic concern with our crop yield results is that they could hide alternate adjustmentsthat help farmers maintain profitability in the face of a changing climate. The US Agri-cultural Census, conducted roughly every 5 years, contains data on overall farm revenuesand expenses for the year in which the census is conducted. A basic measure of profitsfor a given year can be constructed by differencing these two variables (i.e. profits2000 =revenues2000 - costs2000 for years in which data are available, and and this approach asrecently been used in similar settings (Deschenes and Greenstone, 2007).


Figure A.10: Effects of extreme heat on soy yields under various startingyears and differencing lengths.

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Estimates are as compared to the point estimate from a 24-year panel estimated over 1978-2002 displayed by the horizontal line in each figure panel.

We choose not to focus on such a profit measure for two reasons. The first is a concernthat costs are not fully measured, and that unmeasured costs might respond to climateshocks in a way that would bias the above profit measure. In particular, expense datado not appear to include the value of own or family labor, which could respond on theintensive or extensive margin in the face of a drought or heat event (e.g. if a crop failsand is replanted).1 The second concern is that both costs and revenues will likely respond

1In recent years, the value of own labor appears to represent about 10% of operating costsfor corn, based on cost estimates available at http://www.ers.usda.gov/data-products/commodity-


to annual variation in climate, but data are only available for 5-year snapshots. Giventhat our differencing approach seeks to capture change in average farm outcomes overtime, differencing two of these snapshots might provide a very noisy measure of the overallchange in profits.

Regressions appear to confirm that profit measures are quite noisy. Agricultural censusdata on expenditures and revenues are available in 1978, 1982, 1987, 1992, 1997, and 2002.We construct a measure of the change in log profits as:

∆logprofits1980−2000 = ln(profit1997+profit2002)/2−ln(profit1978+profit1982)/2 (A.3)

When we re-estimate our main specification with ∆logprofits1980−2000 as the dependentvariable, the coefficient on extreme heat using the untrimmed sample is β2 = −0.0013,with 95% CI of [-0.010, 0.007], and using the trimmed sample we have β2 = −0.0054, with95% CI of [-0.014,0.003]. This means we can’t reject that there is no effect on profits, andsimilarly can’t reject that the effect of extreme heat on profits is a factor of 3 larger (andmore negative) than the effect on corn yields – i.e. that each additional day of exposureto temperatures above 29C reduced annual profits by 1.4%. This does not provide muchinsight on the relationship between extreme heat exposure and profitability.

We take two alternate approaches to exploring profitability impacts that help to addressthese measurement issues. The first is to construct a measure of revenues using annualyield data, which we multiply by annual data on state-level prices to obtain revenue-per-acre for a given crop. Summing up these revenues across crops then provides a reasonablemeasure of annual county-level crop revenues, which will be underestimated to the extentthat not all contributing crops are included. The effect of climate variation on this revenuemeasure is given in the main text, and we find minimal difference between panel and longdifference estimates of impacts on expenditures.

Our second approach proceeds with the available expenses data from the ag censusto examine the impact of longer-run changes in climate on different input expenditures,where we attempt to capture changes in average expenditures by averaging two censusoutcomes near each endpoint and then differencing these averaged values.2 As shown inTable A.8, we find little effect of long-run trends in climate on expenditures on fertilizer,seed, chemical, and petroleum. While we do not wish to push these expenditure data toofar given the noisy way in which the long differences are constructed, we interpret theseas further evidence that yield declines are economically meaningful and not masking otheradjustments on the expenditure side that somehow reduce profit losses.

costs-and-returns.aspx. Hired labor expenditures are minimal for corn.2As with the profit measure described above, the change in fertilizer expenditures over the

period are constructed as: ∆fertilizer expenditure1980−2000 = (fert1997 + fert2002)/2 - (fert1978 +fert1982)/2


Table A.8: Effects of Climate Variation on Input Expenditures

(1) (2) (3) (4)Fertilizer Seed Chemicals Petroleum

GDD below threshold 0.0005 0.0008∗∗ 0.0011∗ 0.0002(0.0004) (0.0004) (0.0006) (0.0004)

GDD above threshold -0.0007 -0.0009 -0.0001 -0.0009(0.0015) (0.0013) (0.0034) (0.0011)

Precip below threshold 0.0141 -0.0105 0.0392∗∗∗ -0.0016(0.0229) (0.0125) (0.0115) (0.0087)

Precip above threshold -0.0016 -0.0021 0.0004 0.0010(0.0019) (0.0024) (0.0036) (0.0019)

Constant 0.3215∗∗∗ 0.7295∗∗∗ 0.6993∗∗∗ 0.0281(0.0276) (0.0217) (0.0338) (0.0237)

Observations 1528 1519 1523 1518R squared 0.532 0.313 0.460 0.258Fixed Effects State State State StateT threshold 29 29 29 29P threshold 42 42 42 42

Dependent variable is difference in log of input expenditure per acre. All regressions are longdifferences from 1980-2000. All regressions are weighted by average agricultural area between1978-1982. Standard errors are clustered at the state level. Asterisks indicate statisticalsignificance at the 1% ∗∗∗,5% ∗∗, and 10% ∗ levels.

A.8 Exit from agriculture

As an extension to our basic long difference results on how the number of farms change inresponse to climate variation, we adopt an empirical strategy similar to that of Hornbeck(2012a). We use the six agricultural censuses from 1978-2002 to estimate whether thenumber of farms grew differently between areas that were differentially exposed to extremeheating from 1970-1980. We first take the difference between average annual GDD above29◦ from 1976-1980 and average annual GDD above 29◦ from 1966-1970. We then defineextreme heating as an indicator variable for this difference being above a certain value.The econometric specification is,

ln(farms)ist − ln(farms)is1978 = βt ∗ Extremeheatis + αst + εist, (A.4)

where Extremeheatis is an indicator variable for a large change in GDD above 29. Animportant note is that the census defines a farm to be any place where at least $1000 inagricultural products was sold during that year. Table A.9 reports estimates with andwithout state-specific time fixed effects. The state specific time-effect eliminates all state-


specific factors varying over time. For instance, if heating was more heavily concentrated insome states and those states had different policies over time, the state-specific time effectswould control for this correlation. We also show two different definitions of extreme heat.In the first definition it is defined as an indicator for an increase in GDD above 29◦ of10 or more. This results in approximately 48% of counties being classified as having beenexposed to heating. The second definition uses a stricter cutoff of 20. This results in 28% ofcounties being classified as exposed to heating. Each coefficient βt measures the predictedpercentage difference in the number of farms in year t between the counties that warmedfrom 1970-1980 and those that did not. For instance in Column 2, the number of farms in1982 is predicted to be 2.75% lower in counties that heated substantially from 1970-1980.This predicted difference increases to 3.5% in 1987. The predicted difference in the numberof farms generally becomes smaller in the later years of 1997 and 2002 which is consistentwith some longer term adjustments back towards pre-warming degree of farming activity.This interpretation must be made with caution given the large standard errors in theseyears. The pattern of coefficients suggests that simply not farming may be an importantimmediate adaptation to climate change.

A.9 Additional evidence on selection

The potential of exit from agriculture and migration as responses to climate change high-lights an important potential issue with our estimates of the effects of long-term climatetrends on yields. If exit/migration is selective, then the appearance of a lack of adaptationin the data could be due to a selection effect where the most productive farmers recog-nize the changing climate and leave agriculture. In this case the appearance of a lack ofadaptation in the data could be due to the change in the ability of the farming populationthat results from climate change. This possibility would become especially problematic iffarmers that were more productive and had access to better quality land also had a largeropportunity cost of being in farming. If selection of this type is driving our estimates thenwe should see characteristics that are correlated with productivity changing differentiallybetween places that heated and those that did not. In Table A.10 we regress the percentageof farms owing more than $20,000 in equipment on our same climate variables. Since thepercentage of farms owning valuable equipment is positively correlated with yields, if selec-tion is driving our results we should expect to see a large decrease as a response to increasesin extreme temperatures. The results are not consistent with this story. The long differ-ences estimate is negative, but small and not statistically significant from zero. The panelestimate is positive, small in magnitude and marginally statistically significant. While weobviously can not fully rule out selective migration, these regressions are suggestive thatit is not driving our yield results.


Table A.9: Estimated Differences in Log Number of Farms by Amount of Warming

Extreme Heat=Change GDD > 10 Extreme Heat=Change GDD > 20

(1) (2) (3) (4)

1982*Extreme Heating -0.0585∗∗∗ -0.0275∗∗ -0.0741∗∗∗ -0.0230∗∗∗

(0.0177) (0.0107) (0.0231) (0.0057)

1987*Extreme Heating -0.0579∗∗∗ -0.0352∗∗ -0.0727∗∗∗ -0.0455∗∗

(0.0190) (0.0166) (0.0205) (0.0216)

1992*Extreme Heating -0.0351 -0.0396 -0.0460∗∗ -0.0430∗∗

(0.0223) (0.0240) (0.0191) (0.0179)

1997*Extreme Heating 0.0051 -0.0155 -0.0016 -0.0221(0.0296) (0.0318) (0.0216) (0.0171)

2002*Extreme Heating 0.0174 -0.0169 0.0045 -0.0617∗

(0.0351) (0.0299) (0.0352) (0.0318)Observations 12120 12120 12120 12120Mean of Dep Variable -0.13 -0.13 -0.13 -0.13R squared 0.617 0.681 0.618 0.681State by Year Fixed Effects No Yes No Yes

Data are for US counties east of the 100th meridian. Dependent variable in all specifications isdifference between log number of farms in year t and log number of farms in 1978. Coefficientsrepresent estimated differences in log number of farms between counties that experienced extremeheating from 1970-1980 and those that did not. Extreme heating defined as indicator for increasesin GDD above 29 greater than cutoff value of 10 (Columns 1-2) or 20 (Columns 3-4). Allregressions are weighted by county farm area in 1978. Standard errors are clustered at the statelevel. Asterisks indicate statistical significance at the 1% ∗∗∗,5% ∗∗, and 10% ∗ levels.

A.10 Why no adaptation

As described in the main text, Table A.11 provides some evidence that participation in thegovernment insurance program by 2000 was higher in counties who saw large increases inexposure to harmful temperatures (GDD>29C) over the previous two decades, and lowerin counties that saw increase in exposure to generally helpful temperatures (GDD0-29C)over the same period.

A.11 Climate change projections

We derive projected changes in corn productivity due to climate change by combining ourlong differences estimates of the the historical response of corn productivity to climate with


Table A.10: Effects of climate variation on equipment ownership.

(1) (2)Diffs, 1978-1997 Panel, 1978-2002

GDD below threshold 0.0087 -0.0067∗∗∗

(0.0152) (0.0019)

GDD above threshold -0.0178 0.0221∗

(0.0318) (0.0109)

Precip below threshold 0.2114 0.0608(0.1470) (0.0499)

Precip above threshold 0.0524 0.0760∗∗∗

(0.1147) (0.0250)

Constant 9.9251∗∗∗ 74.5041∗∗∗

(0.9928) (6.0013)Observations 1531 7645Mean of Dep Variable 10.50 59.01R squared 0.321 0.324Fixed Effects State Cty, YrT threshold 28 28P threshold 50 50

Dependent variable in Column 1 is the change in the percentage of farms with more than 20KUSD in equipment from 1978 to 1997. Dependent variable in Column 2 is the percentage of farmsowning equipment valued at more than 20,000 USD. Long differences regressions are weighted byaverage farm acres between 1978 and 1982. Panel regressions weighted by average farm acres from1978-2002. Standard errors are clustered at the state level. Asterisks indicate statisticalsignificance at the 1% ∗∗∗,5% ∗∗, and 10% ∗ levels.

climate projections from 18 general circulation models that have contributed to WorldClimate Research Programs Coupled Model Intercomparison Project phase 3 (WCRPCMIP3). Our main projections use the A1B emissions scenario, reported by 18 climatemodels in the CMIP3 database: CCMA, CNRM, CSIRO, GFDL0, GFDL1, GISS.AOM,GISS.EH, GISS.ER, IAP, INMCM3, IPSL, MIROC.HIRES, MIROC.MEDRES, ECHAM,MRI, CCSM, PCM, and HADCM3. For more on these models and their application, seeAuffhammer et al. (2013a) and Burke et al. (2013). The A1B scenario is considered a“medium” emission scenario, and represents a world experiencing “rapid and successfuleconomic development” and a “balanced mix of energy technologies” (Nakicenovic et al.,2000). We choose to explore outcomes under only one emissions scenario both to simplifythe results, and because emissions scenarios diverge much less by mid-century than theydo by the end of the century, meaning our results are less sensitive to the choice of emis-sions scenario than end-of-century projections. Finally, following the climate literature, we


Table A.11: Insurance take-up in 1998-2002 as a function of changes in GDD andprecipitation over 1980-2000.

(1) (2) (3) (4)% Acreage Enrolled log Acres Enrolled Policies Sold Total Premiums

GDD below threshold -0.0006∗ -0.0005 -1.6411∗∗ -3.7636∗∗∗

(0.0003) (0.0006) (0.7021) (1.2821)

GDD above threshold 0.0026 0.0022 8.2093∗ 16.8366∗∗

(0.0018) (0.0025) (4.8110) (7.6828)

Precip below threshold 0.0354∗∗ 0.0309∗∗ -3.3723 57.6410(0.0162) (0.0138) (21.7244) (57.8886)

Precip above threshold -0.0050∗∗ -0.0052∗ -9.3570 -13.4772(0.0019) (0.0025) (10.5879) (17.6880)

log corn area 1.0057∗∗∗

(0.0267)

Constant 0.7929∗∗∗ -0.3736 704.2308∗∗∗ 1250.4442∗∗∗

(0.0237) (0.3035) (43.4052) (86.8633)Observations 1529 1529 1529 1529R squared 0.354 0.955 0.480 0.489Mean Dep. Var. 0.815 9.329 271.227 428.441

The outcome variables are given at the top of each column. Total premiums paid (column 4) are inthousands of dollars. All regressions include state fixed effects, with standard errors are clusteredat the state level. Asterisks indicate statistical significance at the 1% ∗∗∗,5% ∗∗, and 10% ∗ levels.

adopt a “model democracy” approach and assume projections from all models are equallyvalid and should be weighted equally (Burke et al., 2013).

The resolution of these general circulation models is roughly 2.8◦x2.8◦ (about 300kmat the equator), and we map each county in our sample to its corresponding grid cell in theclimate model grids. We derive estimates of climate change by mid-century by calculatingmodel-projected changes in temperature (C) and precipitation (%) between 2040-2059and 1980-1999, and then adding (for temperature) or multiplying (for precipitation) thesechanges to the observed record of temperature and precipitation in a given county. Fortemperature, because our main variable of interest is growing degree days, this requiresadding monthly predicted changes in temperature in a given county to the daily timeseries series in that county, recomputing growing degree days under this new climate, andcalculating the difference between baseline and future growing degree days.

Projections assume a fixed growing season (Apr 1 - Sept 30) and no large shifts in thearea where corn is grown within the US. Area-weighted changes in temperature and precip-itation over US corn area are shown in Figure A.11. The variation in temperature changes


over our 1980-2000 study period span the lower third of the range of model-projected av-erage temperature changes by 2050, and the variation in changes in precipitation in oursample fully span the range of projected average precipitation changes by 2050.

Figure A.11: Projected changes in growing season temperature and precip-itation across US corn growing area by 2050.

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159

Appendix B

Economic shocks and HIVappendix

B.1 DHS Data

Weighting

Sampling weights are used in this paper so that estimated effects represent the averageeffect of the population of interest (the population of 19 sub-Saharan African countries).The sampling weights are constructed as follows.

• Each individual is assigned an inflation factor that is ρ = Ncnc

where nc is the samplesize for survey in which he appears, and Nc is the population of his country in theyear of that survey.

• Further, each individual has a survey-specific inflation factor h that is provided inthe DHS data. h is the inverse probability of his HIV test results being present inthe data. MEASURE DHS calculates h based on an individual’s probability of beingsampled for HIV testing (based on stratification of the survey) and his probabilityof providing a blood sample if requested, based on observable characteristics.

• A composite weight that is the product of ρ and h is employed in all specifications.A robustness check shows that the primary results of this work are not dependenton the use of sampling weights.

APPENDIX B. ECONOMIC SHOCKS AND HIV APPENDIX 160

B.2 Weather data and impact of drought on crop

yields

To help confirm that our measure of recent rainfall shocks is plausibly exogenous andnot correlated with other moments of the rainfall distribution, we regress the number ofrainfall shocks in the past 10 years on the mean, variance, and skewness of each grid’srainfall distribution. Table B.4 presents the results. In all specifications, these correlationsare not significant. In other words, when we estimate across grids, recent rainfall shocksare orthogonal to all three moments of the historical distribution.

While we cannot directly show the importance of rainfall shocks for household income(as noted, the DHS do not include income or consumption measures), aggregate datasuggest that these shocks are economically important. To demonstrate this, we constructa country-level shock measure and estimate it’s impact on maize yields and real per capitaeconomic growth (Data are from Matsuura and Willmott, 2009; FAO,2011, and Heston,Summers, and Aten (2011), respectively). Maize is the most widely grown crop in Africa,and we have data for 41 Sub-Saharan African countries for 1961-2008.1 We similarly havedata on real per capita income growth for these same countries across 1961-2008.

The first four columns of Table B.5 show the impact of rainfall dropping below the 10thor 15th percentile on (log) country-level maize yields across Sub-Saharan African countries,based on panel regressions using country and year fixed effects. Annual maize yields arestrongly affected by precipitation: yields are about 12% lower in a year with rainfall at orbelow the 15th percentile, and 18% lower in a year with rainfall below the 10th percentile.Results are robust to including temperature shocks in the regression. With 60-80% ofrural African incomes derived directly from agriculture, these productivity impacts likelyrepresent significant shocks to household incomes (Davis et al., 2010).2 We repeat thesame regressions using growth in real per capita GDP as the outcome variable (Columns5-8). Negative rainfall shocks again reduce growth rates dramatically, with bigger shocksleading to larger declines in growth rates. We estimate that a 15% shock reduces theeconomic growth rate in that year by 1.8 percentage points, and a 10% shock by 1.9percentage points. This demonstrates again that rainfall shocks exert substantial influenceon economic productivity in Africa.

1The included countries are: Angola, Benin, Botswana, Burkina Faso, Burundi, Cameroon,Central African Republic, Chad, Congo, Cte d’Ivoire, Democratic Republic of the Congo, Eritrea,Ethiopia, Gabon, Gambia, Ghana, Guinea, Guinea-Bissau, Kenya, Lesotho, Liberia, Madagascar,Malawi, Mali, Mauritania, Mozambique, Namibia, Niger, Nigeria, Rwanda, Senegal, Sierra Leone,South Africa, Swaziland, Togo, Uganda, United Republic of Tanzania, Zambia, and Zimbabwe.

2Schlenker and Lobell (2010b) demonstrate that these strong negative impacts of weather shocksgeneralize to other African staples, not just maize.


B.3 Shock Definition

Because by construction the number of shocks in each cluster is fixed across the 40 yearsof rainfall data that we use, one concern is that shocks are therefore mean reverting fromdecade to decade, and that this somehow might bias our results. In this section, we showthat any mean reversion is likely to make our estimates lower bounds on the effect of shockson HIV.

To see this, we first note that HIV is incurable and is thus fairly persistent acrossdecades: while 10 years is a benchmark life expectancy following infection, in fact only50% of those infected will die within 10 years (see appendix figure B.3). Given this fact,consider two clusters, A and B. As constructed, the total number of shocks in each clusteris fixed, such that more shocks falling in one decade leads in expectation to fewer shocks inthe next. Suppose that cluster B had more shocks between 1988-1997 than cluster A andthus higher HIV rates in 1997 compared to A. Given that there is substantial persistence inHIV prevalence over time - HIV is incurable, and average survival after infection is 10 years,meaning that many HIV+ individuals survive for more than a decade - when we measureHIV in 2007 for cluster B, we’ll also be picking up the effects of past shocks (1988-1997).But because our shock measure is (in expectation) negatively correlated across decades,the lower number of shocks in cluster B in 1998-2007 will bias towards zero our estimate ofthe effect of these shocks on 2007 prevalence: we saw fewer shocks in 1998-2007, but higherprevalence due to the previous decade’s shocks. A similar logic holds for Cluster A: thepersistence of HIV means that a low number of shocks in 1988-1997 leads, all else equal,to lower prevalence in 2007, but low shocks in 1988-97 also mean a likelihood of highershocks in 1998-2007. Our estimate of the effect of this higher number of shocks will againbe biased towards zero, because 2007 prevalence in A will be lower due to the low numberof 1988-97 shocks.

As further evidence of the robustness of our shock measure and chosen thresholds, andin the interest of full transparency, Table B.6 provides results from 40 separate estimationsusing different thresholds for the various population sub-samples used throughout the text.The analogous figure for our main results is Figure 2A.

B.4 Estimating sample selection due to

out-migration

In order to estimate the rate at which shocks affect permanent out-migration rates, webegin with an estimate of rural-to-urban migration. For each country in our sample, wecalculate the reduction in rural population (as a share of total population) over a recent10-year period, based on data from the World Bank.3 On average, the rural share of the

3Figures from World Bank Development Indicators, 1990-2000.


populations of these countries is reduced by 5.8% over ten years. Given the wide range ofreasons for migrating to urban areas, migration in response to a shock likely accounts forno more than 20%-30% of this total (van Dijk, Foeken, and van Til, 2001). Nonetheless, weconservatively assume that low-rainfall shocks account for as much as half of this migration,and therefore induce a rural population loss of approximately 2.9% over ten years. Notethat this is the accumulated loss from all shocks occurring during a ten year period.

We use these estimates to back-out the share of population that leaves during eachshock. The column headers in Table B.7 show several possible assumptions of populationloss per shock ranging from 1% to 5%. A bit of algebra reveals that if, for example, 3%of the population leaves during each shock, a village with three shocks over the past tenyears has lost 8.73% of its population in that time. The calculation of lost populationby number of shocks and assumption maintained are shown in the body of table B.7. Byapplying these calculations to the rural clusters in our data according to each cluster’snumber of shocks, we calculate the total population lost in our rural sample over the tenyears preceding the survey. The bottom row of table B.7 shows these estimates of totalpopulation loss over a ten year period.

The second column, which assumes that 2% of the population leaves per shock predictsthat the rural sample has lost 2.91% of the population over the ten year period. Thisprediction aligns the best with the estimate that rural areas lose 2.9% of population todrought-induced migration over a ten year period. Therefore 2% loss per shock is theassumption maintained. Notice that, if we assume that all out-migration is shock induced(i.e. 5.8% loss over 10 years), this would suggest 4% population loss per shock. We thereforetake 4% loss per shock as our extreme upper bound.

B.5 Considering shock timing

In this appendix, we consider whether shocks occurring within the past ten years differ intheir impacts on the HIV epidemic according to whether they occurred relatively early orlate during that period. We begin by simulating a model of the epidemic and then observethe impact of simulated shocks at various points in time.

Simulating the epidemic

We simulate an epidemic broadly representative of the high prevalence countries in oursample in the following way. In 1950, one person is infected in a country with a populationof 25 million.4 Each year, the newly infected individuals infect, on average, 1.2 otherindividuals (Pinkerton, 2008). Those infected more than 1 year ago infect another with an

4The first documented case of HIV in SSA was in 1959, suggesting that the virus mutatedbetween 1910 and 1950 (Zhu et al, 1998; Worobey et al, 2008). Our survey countries’ averagepopulation is 22 million.


annual probability of 0.1 (Pinkerton, 2008). Each cohort of new infections dies at a ratethat is specific to the years since their seroconversion (Fig. B.3).

At the end of each year, the number of infections is given by the number of infections atthe end of the previous year, minus the deaths in the current year (from previous cohorts),plus the year’s cohort of new infections.

In 1990, when prevention efforts began en masse, the annualized probability of trans-mission drops to 0.6 for individuals with an acute infection, and 0.04 for individuals with achronic infection (¿1 yrs since seroconversion). The “current year” (or year of observation)is 2005, which is the mean and median of our data years. The simulated epidemic is shownfrom 1970 to 2005 by the black line (labeled “Model”) in Fig. B.4. Notice the dashed lineat 1995; this serves as visual reference for comparing the post-1995 trend to the graphs ofcountry prevalence in Fig. B.2.

When the simulation ends in 2005, there are 3.8m People Living with HIV (PLWH),yielding a prevalence of 16.5%. Of these, the number that were infected in each of theprevious 18 years is calculated (note that none survives year 19 in the model). The CDFin Fig. B.5 shows that for PLWH, more than 80% were infected in the past 10 years.One might consider extending the time period of analysis to 18 years to capture 100% ofinfections, but notice that for those infected 11-18 years ago, only 20% are currently alive(see Fig. B.3).

Role of shock timing

New infections in each year are a function of new infections in previous years. Therefore,a shock that increases incidence in 1995 will indirectly increase incidence in each of thefollowing 10 years (when observing in 2005). In contrast, a shock in 2000 will only affectthe incidence of the following 5 years until 2005. Shocks further in the past should havegreater impacts on current prevalence (conditional on the shock being within the past 10years).

The red and blue lines in Fig. B.4 depict simulations of shocks to incidence that occur8 years prior (“early”) and 2 years prior (“late”) to the end-point of 2005, respectively. Ineach shock, the annual transmission probabilities increase to 0.7 and 0.04 for acute andchronic infections, respectively, during the year of the shock and the following year. It isclear that the path of prevalence between 1996 and 2005 differs significantly in the twoscenarios. Given a shock of the same size and duration, the earlier shock increases 2005prevalence by 50% more than does the later shock (1.7 percentage points vs. 1.1 ppts).

This suggests that shocks occurring 6 to 10 years ago will exhibit a stronger impact oncurrent prevalence than will shocks that have occurred in the past 5 years.


B.6 The role of ARV Access

The number of people in sub-Saharan Africa being treated with ARVs has increased dra-matically during the 2000 to 2009 period. This is due to both increased funding by PEPFARand the Global Fund as well as substantial reductions in procurement costs (WHO, 2006;Friedman, 2012). Figure B.6 presents ARV coverage rates on a country level for when datais first available (2004) up until the year of the DHS survey. ARV coverage rates (thepercentage of those receiving ARVs who are in need) are below 40% for all countries in oursample time frame. In rural areas, where we identify the effects that shocks have on HIVrates, ARV coverage rates are even lower. Access to ARVs is more limited for individualsliving in rural areas due to both resource constraints and fewer trained medical profession-als (van Dijk et al., 2009), as well as the greater distances that rural individuals may haveto travel to access ARVs at clinics (Ojikutu, 2007). A number of country-specific studiessubstantiate this claim. In Kenya, ARVs were first targeted at urban areas and regionswith high HIV prevalence (Friedman, 2012), longer travel times make it more difficult toaccess ARVs in rural areas in Zambia (van Dijk et al., 2009), and overall access to healthservices (including ARV access) is much more limited in rural than urban Mozambique(Groh et al., 2011).

One concern might be that shocks are correlated with ARV access which could leadto a different interpretation of our main results. For example, if ARVs are more readilyavailable in areas with shocks then our results might be explained by more HIV+ individualsliving longer in areas with shocks. Unfortunately sub-national data on ARV availabilityis not available for our sample. The DHS does ask “Have you heard of drugs to helpinfected people to live longer?” in select countries, which we use as a crude proxy for ARVaccessibility. We find that our shock measure is not correlated with ARV awareness whichsuggests that ARV access and shocks are not correlated (Table B.8).

B.7 Estimating Changes in Sexual Behavior

To investigate the plausibility of coping behaviors as the link between rainfall and HIV, weestimate the changes in underlying sexual behavior that would be needed to generate theobserved increases in HIV. To back out the actual change in underlying sexual behavior asa result of shocks, we follow the methodology developed by Gong (forthcoming) to estimatethe change in sexual partnerships that would result in the 0.9 and 0.6 ppt increases in HIVinfection reported in Table 3.3, Column 6.5 As with all modeling exercises that involvesexual behavior and HIV infections, the estimates generated are sensitive to the parameter

5We focus on the change in number of sexual partnerships following Kaplan (1990), Kremer(1996), and Oster (2005).


values. For these, we rely on values from the health and epidemiological peer-reviewedliterature.6

For men, we estimate that each shock leads to an increase of .65 partners, which is aboutone-eighth of the mean number of lifetime partners for men; 95% CI (.61,.69) For women,the model suggests an additional 1.42 partners per shock would be needed to generatetheir .9 ppt change in HIV infection; 95% CI (1.30,1.53). In this sample, women reporton average 2.2 lifetime partners. Based on clinical trials using prostate-specific antigen,which detects sexual activity in the past 48 hours, Minnis et al. (2009) showed that womenin Zimbabwe under-report sexual behavior by about 50%. This suggests an average of 4.4lifetime partners per woman. Annualizing based on the average woman in the sample (age28 with sexual debut at 16), this averages to about one partner every three years.

B.8 Country-level prevalence

To explore the relevance of shocks for the broader patterns of HIV prevalence across Sub-Saharan Africa, we run simple cross-sectional regressions relating prevalence at the end ofeach decade to accumulated shocks over the previous decade. Country-level HIV prevalenceis estimated as a function of number of shocks over previous 10 years for the 38 countries inSub-Saharan Africa with HIV data.7 Details on the AIDS data are provided in UNAIDS(2010). Shocks are the sum of rainfall realizations below the 15th percentile, based onannual country-average rainfall (weighted by crop area). Country HIV prevalence data arefrom UNAIDS.

6The model used to estimate changes in sexual behavior uses a simple transformation of theAVERT model (Rehle et al., 1998).

M =log(1− P (HIV Infection))

log(W [1−R(1− FE))N + (1−W ))(B.1)

where P (HIV Infection) is the likelihood of HIV infection, W =HIV prevalence, R = HIVtransmission per unprotected coital act, F =fraction of sexual acts where a condom is used, E =effectiveness of condoms at reducing HIV transmission, N = Number of sex acts per partner, andM= Number of sexual partners. Further information about parameters employed is available fromthe authors on request.

7The countries included in these regressions are: Angola, Benin, Botswana, Burkina Faso,Burundi, Cameroon, Central African Republic, Chad, Congo, Cte d’Ivoire, Eritrea, Gabon, Gambia,Ghana, Guinea, Guinea-Bissau, Kenya, Lesotho, Liberia, Madagascar, Malawi, Mali, Mauritania,Mozambique, Namibia, Niger, Nigeria, Rwanda, Senegal, Sierra Leone, South Africa, Swaziland,Togo, Uganda, United Republic of Tanzania, Zambia, and Zimbabwe.


Figure B.1: Countries included in the study. Darker shades correspondingto higher HIV prevalence.


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Table B.1: DHS Sampling for Serostatus Testing

Country Year Men Aged Women Aged

Testing in all sampled householdsMozambique 2009 12-64 12-64Swaziland* 2007 15-49 15-49Tanzania 2004, 2008 15-49 15-49Liberia 2007 15-49 15-49Zimbabwe 2006 15-54 15-49Zambia 2007 15-59 15-49Ghana 2003 15-59 15-49

Testing in random 50% of sampled householdsSierra Leone** 2008 6-59 6-59Kenya 2003, 2009 15-49 15-49Lesotho 2004 15-59 15-49Cameroon 2004 15-59 15-49Congo DR 2007 15-59 15-49Ethiopia 2005 15-59 15-49Guinea 2005 15-59 15-49Rwanda 2005 15-59 15-49

Testing in random 33% of sampled householdsMalawi 2004 15-54 15-49Burkina Faso 2003 15-59 15-49Mali 2006 15-59 15-49Senegal 2005 15-59 15-49

* Swaziland: additional HIV testing for those aged 12-14 and 50+ in a random 50% of

sampled households. ** Sierra Leone: Individual questionnaires were administered only to

those aged 15-49 (59 for men)


Table B.2: Non-response for Serostatus Testing

Men WomenCountry Year Tested Refused Tested Refused

Lesotho 2004 68% 16.6% 81% 12.0%Swaziland 2007 78% 16.6% 87% 9.5%Zimbabwe 2006 63% 17.4% 76% 13.2%Malawi 2004 63% 21.9% 70% 22.5%Mozambique 2009 92% 6.1% 92% 6.1%Zambia 2007 72% 17.6% 77% 18.4%Cameroon 2004 90% 5.6% 92% 5.4%Kenya 2003 70% 13.0% 76% 14.4%Kenya 2009 79% 7.8% 86% 8.2%Tanzania 2008 80% 8.0% 90% 6.3%Tanzania 2004 77% 13.9% 84% 12.3%Burkina Faso 2003 86% 6.6% 92% 4.4%Congo DR 2007 86% 5.7% 90% 4.4%Ethiopia 2005 75% 12.6% 83% 11.2%Ghana 2003 80% 10.7% 89% 5.7%Guinea 2005 88% 8.5% 93% 5.0%Liberia 2007 80% 11.3% 87% 7.3%Mali 2006 84% 4.8% 92% 3.2%Rwanda 2005 96% 1.9% 97% 1.1%Sierra Leone 2008 85% 5.5% 88% 4.7%Senegal 2005 76% 16.0% 85% 9.9%

Average 79% 11% 86% 9%

Rates are for the full HIV testing sample, with the exception of Mozambique. Rates for MZ

are for the 15-49 sample. Rates are those reported in the DHS final reports for each survey,

as the outcome of HIV measuring at the individual level is not included as an indicator in

most data sets.


Table B.3: Non-response is not correlated with Shocks

Selected but Selected butDependent Variable –¿ Refused Refused not tested not tested

(1) (2) (3) (4)

Num. shocks past 10 yrs. -.002 -.002 .001 .001(.005) (.004) (.003) (.003)

Indiv. controls No Yes No Yes

Mean of Dep. Var .100 .100 .118 .11895% CI for coeff (-.011, .007) (-.009, .006) (-.006, .008) (-.005, .006)

Observations 70547 70547 190794 190794R2 .026 .034 .032 .045

Note: Whether or not a selected individual refused an HIV test is the dependent variablein columns 1 and 2. The outcome of the test request, including refusal and failure to testfor other reasons is given only for women in the following surveys: 2005 (ZW), 2006 (ML,SZ), 2007 (DRC, LB, ZM), 2008 (SL, KE), is given for men and women in 2007 TZ, andis not given at all in the remaining 12 surveys. For this reason, columns 3 and 4 employall surveys and use lack of HIV test result as the dependent variable. Recall that only asub-sample of households were selected for the men’s survey and HIV testing (see section3.3), and we endeavor to include only individuals from these households in this analysis.Selection into the sub-sample is not indicated in the data, and thus these households areonly identifiable by the existence of an interview with, or a test result from, a male in thehousehold. For households without data on a male, we are not able to identify the selectedhouseholds (some households were selected but had no male present, for example). Thesample employed in columns 3 and 4 includes all individuals in households that have dataon a male in any of the surveys. These individuals were definitely selected for HIV testing,though they are not all of the individuals selected for testing.

The estimates suggest a fairly precise zero effect of shocks on test refusal or non-response.

Based on the 95% confidence intervals, we can reject that a shock affects testing rates by

more than one percentage point.


Table B.4: Rainfall Shocks and Overall Variability

Dependent Variable: Number of 15% rainfall shocks in past 10 years.

(1) (2) (3) (4)

mean .000 .000(.000) (.000)

variance -.000 -.000(.000) (.000)

skew -.181 -.128(.143) (.167)

Observations 1701 1701 1701 1701R2 .181 .182 .185 .194

Estimation at the grid level, with country fixed effects. Robust standard errors are shown

in parentheses, clustered at the country level.


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Table B.6: Vary Shock Definition: 10 to 20%

Dependent Variable: HIV Infection

Pct Shocks Rural & High PrevalenceThreshold All Rural All Women

(1) (2) (3) (4)10% 0.002 0.003 0.007 0.009*

(0.002) (0.002) (0.005) (0.005)11% 0.002 0.003 0.007* 0.008*

(0.002) (0.002) (0.004) (0.004)12% 0.002 0.003* 0.007* 0.009**

(0.002) (0.002) (0.004) (0.004)13% 0.002 0.003* 0.007* 0.009**

(0.002) (0.002) (0.004) (0.004)14% 0.002* 0.003* 0.007** 0.009**

(0.001) (0.002) (0.003) (0.004)15% 0.003* 0.003** 0.008** 0.010***

(0.001) (0.002) (0.003) (0.004)16% 0.002 0.003* 0.007** 0.009**

(0.001) (0.002) (0.003) (0.004)17% 0.002 0.003* 0.006* 0.008**

(0.001) (0.002) (0.003) (0.004)18% 0.002 0.003* 0.006* 0.007**

(0.001) (0.002) (0.003) (0.004)19% 0.001 0.002 0.004 0.006*

(0.001) (0.002) (0.003) (0.003)20% 0.001 0.002 0.004 0.005

(0.001) (0.002) (0.003) (0.004)

N 202,216 134,874 77,760 43,147

Each cell represents a separate regression, with the row indicating the threshold at which a

shock is generated and the column indicating the sum-sample employed. All specifications

include controls for gender, age and survey fixed effects. Estimations are weighted to

be representative of the 19 countries. Robust standard errors are shown in parentheses

clustered at the grid level.


Table B.7: Potential Loss in Rural Populations due to Shock-induced Migration

Out-migration Per Shock: 1% 2% 3% 4% 5%

Shocks over 10 yrs 10-yr population loss

0 0.00% 0.00% 0.00% 0.00% 0.00%1 1.00% 2.00% 3.00% 4.00% 5.00%2 1.99% 3.96% 5.91% 7.84% 9.75%3 2.97% 5.88% 8.73% 11.53% 14.26%4 3.94% 7.76% 11.47% 15.07% 18.55%5 4.90% 9.61% 14.13% 18.46% 22.62%6 5.85% 11.42% 16.70% 21.72% 26.49%7 6.79% 13.19% 19.20% 24.86% 30.17%

Estimate of 10-yr reductionin population based on numberof shocks observed in our data 1.46% 2.91% 4.33% 5.74% 7.13%

Each cell represents the ten-year population loss in a cluster that has occurrences of shocks

as given by the row, and population loss per shock as given by the column. The last

row represents the assumed total 10-year loss from the rural sample as a whole based on

the shocks observed in the data. The highlighted columns best match our rural-to-urban

migration estimates that (col. 2) rural areas lose approximately 2.9% of population over

the course of ten years due to drought-induced migration and (col. 4) villages lose 5.8% of

population over the course of ten years due to total (all-cause) migration.


Figure B.3: Survival Following Seroconversion (East African populationwithout ARV)


Figure B.4: Epidemic Curve

Table B.8: ARV Awareness and Shocks

(1) (2) (3)All Rural Rural& High Prevalence

Num. shocks past 10 yrs. -.002 -.001 .007(.006) (.006) (.006)

Observations 89208 55336 43082R2 .304 .337 .101Mean of Dep. Var .658 .633 .819

Sample includes: Congo DR, Liberia, Malawi, Mozambique, Sierra Leone, Swaziland, Tanzania

(2008), Zambia, and Zimbabwe. Column headers indicate sample employed. Specifications include

controls for gender and age, rural/urban designation (where applicable), and survey fixed effects.

Estimations are weighted to be representative of the 19 countries. Robust standard errors are shown

in parentheses clustered at the grid level.


Figure B.5: People currently living with HIV, by year of seroconversion


Figure B.6: ARV Coverage Rates (2004-2009)

2004 2005 2006 2007 2008 2009 2010

0

10

20

30

40

50

Low Prevalence

AR

V c

over

age

(%)

● Guinea ● Liberia

● Mali

● Rwanda

● Sierra Leone

● Senegal

2004 2005 2006 2007 2008 2009 2010

0

10

20

30

40

50

High Prevalence

AR

V c

over

age

(%)

● Cameroon

● Lesotho● Malawi

● Mozambique● Swaziland

● Zambia

● Zimbabwe

ARV Coverage rates from the World Bank Development Indicators. Black dots indicate the year

of the DHS survey used for each country.

Table B.9: Shocks predict country-level HIV prevalence

(1) (2) (3) (4)levels 1990s levels 2000s change 1990s change 2000s

Num. shocks in past 10 yrs 2.089∗∗ 2.450∗∗∗ 1.250 0.408∗

(0.887) (0.788) (0.798) (0.234)Observations 37 37 36 37R2 0.140 0.216 0.064 0.068Mean dep. var. 7.0 6.3 4.6 -0.7

Regressions marked “levels” have HIV prevalence in either 1999 (model 1) or 2008 (model 2)

as the dependent variable; Regressions marked “changes” have as the dependent variable

the change in HIV prevalence over the previous decade, with the end year either 1999

(model 3) or 2008 (model 4). Regressions include the 38 Sub-Saharan African countries

with data in the UNAIDS database.

179

Appendix C

Climate and conflict appendix

C.1 Study selection, reanalysis and evaluation

Our conclusions from the literature are based only on those studies that implement Eq.1 from the main text or one of the mentioned alternatives. In select cases, studies didnot meet this criteria but the data from these analyses were publicly available or suppliedby the authors. In these cases, we reanalyzed the data from the original analysis usingthis common method. Table 1 lists the 60 studies that met this criteria initially or werereanalyzed, and upon which we base our conclusions.

Following the norms of social science where publication lags are long – often on theorder of several years – we include archived working papers that have not yet been publishedin journals. This standard is important because journals may exhibit a publication biasby underreporting null results and because research on this topic has expanded rapidly inthe last few years, with half the studies released since 2011. After their careful review, wedecided to include 16 unpublished working papers as primary studies to ensure our analysisis as up-to-date as possible. The inclusion of these studies does not drive our findings andour conclusions would continue to hold even if they were omitted. For example, of the 27estimates for the effect of temperature on modern human conflict, 21 come from publishedstudies and all 21 indicate that higher temperatures are associated with higher rates ofconflict. If there were no causal relationship between warming and conflict, obtaining 27estimates agreeing in a positive association would be extremely unlikely to occur fromsampling variability alone. If we were to omit the four unpublished estimates then wewould obtain agreement in sign across 21 published studies, still a very unlikely event tooccur by chance.

Similarly, we note that while the authors of this analysis are active researchers in thisfield, our own contributions are modest in comparison to the collective output of the globalresearch community. By our count, at least 190 authors from around the world conductedthe 60 primary studies that we analyze here, of which only five Miguel, Satyanath, and

APPENDIX C. CLIMATE AND CONFLICT APPENDIX 180

Sergenti (2004b); Miguel (2005); Mehlum, Miguel, and Torvik (2006); Burke et al. (2009a);Hsiang, Meng, and Cane (2011) are products of our own efforts in collaboration with coau-thors that did not participate in this analysis. In this review, we critically revaluate ourown work, in light of more recent methodological advances and published criticisms (seeTable 1 and below) and in three out of five cases returned to our original data Miguel,Satyanath, and Sergenti (2004b); Miguel (2005); Burke et al. (2009a) to reanalyze it. Inone case Miguel (2005) we found it appropriate to focus on conclusions weaker than theresults emphasized in the original study to ensure that our inferences from the study wereconsistent with the rigorous methodological standards we adopt here (although, note thatthe result presented here was also presented in the original study). We also point out that ifour five studies were omitted from this analysis then our overall conclusions would remainunchanged.

Below we provide additional details on the papers appearing in Fig. 4-5 (a subset ofwhich appear in Fig. 2), including the econometric specification used for each, and themethod and reason for reanalysis in cases where it was done.

Our strict methodological standards led us to exclude several studies, some of whichreported an association between climate and conflict and some of which reported no as-sociation (see Section A.2 below). Because reanalysis of previous studies is often difficultand time-intensive, it is neither cost-effective nor reasonable to reanalyze all studies thatfailed to meet our standards. In determining which studies merited reanalysis, we selectedstudies that presented unique data sets that were not analyzed according to our standardselsewhere, that were structured such that Eq. 1 could be estimated, and for which data andreplication code was available. For the sake of transparency, we describe below why severalpublished studies were not reanalyzed here. We also note that while reanalysis caused thebody of literature as a whole to appear more consistent than previously thought, it did notuniformly cause all studies to exhibit a stronger association than was originally reported –the results of some studies that reported a climate-conflict relationship were weakened byreanalysis (for examples, refs. Levy et al. (2005); Fjelde and von Uexkull (2012)).

Papers appearing in Fig. 4-5

• Auliciems and DiBartolo 1995 Auliciems and DiBartolo (1995). We compute theaverage response across days in each week by dividing day-of-week-specific coefficientsreported in their Table 3 by day-of-week-specific average CALLS reported in theirTable 1 and then averaging across days.

• Bergholt and Lujala 2012 Bergholt and Lujala (2012). We use replication data toestimate Model 12 in their Table V, dropping the outcome variable covariate (percapita GDP). Standard errors are clustered at the country level. The coefficient


on population affected by natural disasters is essentially unchanged from what isreported in their table.

• Bohlken and Sergenti 2011 Bohlken and Sergenti (2010). We use replication datato estimate the reduced form version of Model 2 in their Table 4, and focus on thecontemporaneous effect of rainfall on the number of riots. We estimate the modelwith state and year fixed effects but without the additional controls, and cluster theerrors at the state level. The p-value on the contemporaneous rainfall coefficient wereport is p = 0.124.

• Bruckner and Ciccone 2011 Bruckner and Ciccone (2011). We report results fromModel 1 in their Table 3.

• Buhaug 2010 Buhaug (2010b). This paper and a companion paper Buhaug (2010a)challenge earlier results in Burke et al. 2009 Burke et al. (2009a). Many of theresults presented in these papers are based on research designs that did not meet ourcommon standard: they do not control for location fixed effects1 or time trends, theyinclude outcome variables as covariates, and they misinterpret statistical uncertainty.The new result in these papers that meets our methodological criteria is to show thatthe statistical significance of the temperature result in Burke et al. depends on themortality threshold used for defining conflict.

In Fig. 4, we report the finding in Model 3 in Table 1 in ref. Buhaug (2010b),focusing on the contemporaneous effect of temperature on conflict incidence. This isthe median standardized effect size across seven different estimates given in BuhaugBuhaug (2010b,a) that meet our criteria. We plot these estimates in Fig. C.1, alongwith the range of comparable estimates from Burke et al Burke et al. (2009a, 2010c).Confidence intervals on most estimates are wide, and only 2 out of 14 estimates(14.3%) can reject a standardized effect size of 10% per 1σ. Models in SupplementaryFig. C.1 with stars (**) are those that are shown in Fig. 5. Following critiques inref. Buhaug (2010b), we also include a model using data from the full 1981-2008period that was not reported in ref. Burke et al. (2010c); the standardized effect inthis estimate is nearly identical to the main result in Burke et al 2009, albeit with asomewhat wider confidence interval.

• Burke et al 2009 Burke et al. (2009a). We report results from Model 2 in their Table1, focusing on the contemporaneous effect of temperature. This is shown in Fig. C.1,labeled with “**”. Standard errors are clustered at the country level.

1Buhaug Buhaug (2010a) explicitly argues that fixed effects should not be included in theanalysis, however in our reanalysis we conduct an F-test to jointly test the significance of the fixedeffects – if the fixed effects were similar, it is possible that their omission could be justified in thisspecial case. However, this F-test rejects the hypothesis that country fixed effects are the sameacross countries (p<0.001) indicating that they should not be omitted from the model.


Figure C.1: Standardized effect sizes in Buhaug (2010b,a) and Burke et al.(2009a, 2010c).

% c

hang

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r 1σ

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in c

limat

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el 4

Each marker represents the estimated effect of a 1σ increase in a climate variable, withthe magnitude of the response expressed as a percentage change in the outcome variable,relative to the mean conflict rate. Whiskers represent the 95% confidence interval on thispoint estimate. Colors and marker shapes are as in Fig. 5, and dashed line is the median

estimate from Fig. 5. Estimates marked with “**” are shown in Fig. 5. The selectedestimate from Buhaug is his median estimate while the selected estimate from Burke et al.

is their primary specification, which is below their median estimate.


• Burke 2012 Burke (2012) (who we note is not related to the author of this article)originally used temperature and rainfall as instrumental variables for the effect ofeconomic growth on leadership exit. Burke reported the reduced form effect of cur-rent and lagged temperature and rainfall on leadership exit in a model that containedoutcome variables as covariates (their Table 3). Following the author, we use datafrom the author to estimate a linear probability model for leadership exit:

leader exitit = β1tempit+β2tempi,t−1+β3precit+β4preci,t−1+µi+ θi×t+εit (C.1)

where i=country, t=year, µi is a country fixed effect, and θi is a country-specifictrend. leader exit is a dummy variable for any leader exit and temp and prec aretemperature and precipitation variables, all are described in their paper. Errors areclustered at the country level. We focus on the contemporaneous effect of tempera-ture. The p-value on the temperature coefficient we report is p = 0.06.

• Burke and Leigh 2010 Burke and Leigh (2010) (we note that the former is not relatedto the author of this article) originally used temperature and rainfall as instrumentalvariables for the effect of economic growth on democratic-change events. The authorsdo not report the reduced form effect of these instruments. Following the authorsinstrumental variables specification and notation (Table 4, Model 2), we use thereplication data to estimate

demchangeeventit =β1tempdevnew1interacti,t−1 + β2tempdevnew1interacti,t−2

+ β3precipitationinteracti,t−1 + β4precipitationinteracti,t−2

+ µi + θt + εit

where i=country, t=year, µi is a country fixed effect, and θt is a country-specifictrend. demchangeevent is a dummy variable for democratization events and tem-perature and precipitation are represented by the variables tempdevnew1interactand precipitationinteract, as described in their paper. Errors are clustered at thecountry level. We focus on the one-year lag effect of temperature and precipitation,which are implicitly the focus of the authors who use these variables to instrumentfor one-year lagged income growth. We find that the effect of temperature on de-mocratization events (β1) is positive, large and statistically significant (p= 0.03) forthe full sample (shown in Fig. 5). When we restrict the sample to countries thatare initially autocratic, which is the sample that the authors focus on, the effectbecomes 15% larger but also slightly less precisely estimated (p=0.06). The effect ofprecipitation (β3) is negative, consistent with other analyses, but it is not statisticallysignificantly different than zero (p=0.50).

• Card and Dahl 2011 Card and Dahl (2011). We report results from a version ofModel 3 in their Table 4, where we obtained replication data from the authors andre-estimated the regression with only the “hot” and “cold” weather variables as


covariates. “Hot” is a dummy variable indicating a maximum daily temperatureabove 80F. The coefficient on the “cold” dummy variable (a day below 32F), whichwe do not display, is negative and also significant: cold temperatures reduce domesticviolence in their data by about the same amount. Following the authors, standarderrors are clustered by the team-season. Estimating the model with OLS instead ofpoisson regression delivers coefficients that are slightly larger and more statisticallysignificant, and coefficient estimates including their full set of football score covariatesdelivers similar results. We report the smaller and marginally significant poissoncoefficients (p = 0.06).

• Couttenier and Soubeyran 2012 Couttenier and Soubeyran (2013). We report resultsfrom Model 3 in their Table 2.

• Dell, Jones, and Olken 2012 Dell, Jones, and Olken (2012b). We report results fromModels 4 and 5 in their Table 6, for civil war onset and irregular leader transition,respectively. Following the authors, standard errors are two-way clustered at thecountry level and at the year level.

• Fjelde and von Uexkull 2012 Fjelde and von Uexkull (2012). We use data from theauthors to estimate Model 5 in their Table 1 with OLS and include location fixedeffects and year fixed effects, dropping their outcome variable covariates. Standarderrors are clustered at the location level (first administrative level). Marginal effectsare somewhat smaller than what they report and standard errors are larger, causingtheir results to be marginally statistically significant after reanalysis. The p-valueon the coefficient we report is p = 0.09.

• Harari and La Ferrara 2013 Harari and La Ferrara (2013). The updated (2013)version of their working paper does not include a model with cell fixed effects, sowe retain the estimate from the earlier (2011) version of the paper with cell fixedeffects. After discussions with the authors, we report results from Model 1 in theirTable 4 in their 2011 paper, focusing on the contemporaneous effect of SPEI (the“Standardized Precipitation-Evapotranspiration Index”). We note that in this ver-sion of the paper, a higher SPEI indicates less drought-like conditions, such that therelationship between SPEI and conflict is negative.

• Hendrix and Salehyan 2012 Hendrix and Salehyan (2012). We re-estimate theirresults in Model 7 in Table 3 with OLS and country fixed effects and year fixedeffects, dropping the additional control variables. Standard errors are clustered at thecountry level. To make results comparable with other studies, we follow Hidalgo etal and use the absolute value of rainfall deviations from the mean as the independentvariable.

• Hidalgo et al 2010 Hidalgo et al. (2010b). We report results from Model 7 in theirTable 3. Errors are clustered at the municipal level.


• Hsiang, Meng, and Cane 2011 Hsiang, Meng, and Cane (2011). We report resultsfrom Model 3 in the their Table 1, focusing on the effect for teleconnected regions.

• Jacob, Lefgren, and Moretti 2007 Jacob, Lefgren, and Moretti (2007). We reportresults from the first columns of Panel A and B in their Table 1, which we re-estimateusing data from the authors. Following the authors, regressions are weighted bycounty average crime levels. To account for spatial and temporal correlation, wecluster the standard errors by both jurisdiction and state-year.

• Larrick et al 2011 Larrick et al. (2011). Using data from the authors to estimate thelinear probability model

hit batterijdt = βtempjdt + µj + θt + εijdt (C.2)

where i=is an at-bat, j=ball park, d=day of game, t=year, µj is a park fixed effect,and θt is a year fixed effect. hit batter is a dummy variable that is one if a batteris hit by the pitcher. Errors are clustered at the game level. Because Larrick et alfocus on retaliation against batters and interact temperature variables with factorvariables describing the number of previously struck batters, we restrict the sampleto those at-bats when retaliation is possible, i.e. plays when the batter’s pitcher hadpreviously hit a batter on the opposing team.

• Levy et al 2005 Levy et al. (2005). We use data from the authors to reestimate thelinear probability model

any conflictijt = βWASPijt + µi + θt + εijt (C.3)

where i=grid cell, j=country, t=year, µi is a grid-cell fixed effect, and θt is a yearfixed effect. any conflict is a dummy variable that is one if any conflict is estimatedto begin in the cell and WASP is the Weighted Anomaly Standardized Precipita-tion index, where both variables are described in their paper. Errors are two-wayclustered, at the country-by-year level to account for spatial correlation and at thegrid-level to account for serial correlation. The p-value on the coefficient we reportis p=0.10.

• Maystadt, Ecker, and Mabiso 2013 Maystadt, Ecker, and Mabiso (2013). We reportresults from Column 1 in their Table 1. Errors are clustered at the administrativeregion level.

• Miguel, Satyanath, and Sergenti 2004 Miguel, Satyanath, and Sergenti (2004b). Wereport results from column 1 in their Table 3, focusing on the role of lagged precip-itation, with errors clustered at the country level. We report this result in additionto Burke et al 2009 because Miguel et al focus on a different outcome (civil conflictrather than civil war) and a different climate variable (rainfall growth rather than


temperature). Using a different climate dataset, Burke et al 2009 find that the effectof precipitation is no longer significantly different from zero once temperature is in-cluded in the regression; however, using the original precipitation data in Miguel etal 2004 and including the temperature data from Burke et al 2009 yields a precipi-tation coefficient statistically indistinguishable from what we report here. Thus weretain the Miguel et al result as a unique result.

• Miguel 2005 Miguel (2005). We report results from column 5 in his Table 4. Standarderrors are clustered at the village level. The p-value on the coefficient we report is p= 0.14.

• O’Laughlin et al 2012 O’Loughlin et al. (2012). In their main specifications reportedin the paper, the authors do not control for location fixed effects, and they includeoutcome variables as covariates (although they show in an appendix that their tem-perature results are robust to including the location fixed effects and to droppingoutcome variables from their controls). Because the authors use monthly data, anadditional concern is that the authors have not accounted for seasonality: certainmonths in the year could be both warmer and have higher conflict for some unob-served reason (e.g. perhaps conflict always happens in the non-harvest season). Toaccount for this, we follow Ranson Ranson (2012) and include grid cell-by-monthfixed effects, which accounts for any seasonality in each grid cell. Preserving thevariable names in their replication files, we estimate the following specification:

eventsimt = β1spi6imt + β2ti6imt + µim + θt + εimt (C.4)

where i=grid cell, m=month, t=year, µim is a grid-by-month fixed effect, and θt is ayear fixed effect. events, spi6, and ti6 are the conflict, precipitation, and temperaturevariables as defined in their paper and replication files. Errors are two-way clusteredat the country-by-year level to account for spatial correlation and at the grid-levelto account for serial correlation. The β’s are thus estimated from within grid cellvariation over time, accounting for any seasonality in climate or conflict within eachgrid, and accounting for any trends in climate or conflict over the study period acrossthe region as a whole. We find that the authors’ results for temperature are robust,but that their precipitation results are no longer statistically significant. Estimatingthe model with country-by-year fixed effects, which would allow for non-parametriccountry-level trends in climate and conflict, yields quantitatively similar results fortemperature.

• Ranson 2012 Ranson (2012). To make results comparable to other studies, we usedata from the author to replicate Columns 1, 2, and 4 in his Table 2 but replacethe binned temperature and precipitation variables with simpler linear specifications;we include maximum temperature and precipitation (and their lags) as regressors,in addition to his county-by-month and county-by-year fixed effects. Following the


author, regressions are weighted by county population. Errors are clustered two-ways, at the state-by-year level to account for spatial correlation and at the county-level to account for serial correlation.

• Sekhri and Storeygard 2012 Sekhri and Storeygard (2012). We report results fromColumn 1 in Table 2 (dowry deaths) and Column 1 in Table 3 (domestic violence).

• Theisen 2012 Theisen (2012). The original result did not include both temperatureand precipitation in the same regression and did not report the marginal effect oftemperature in their Table 1 or Fig. 2, where marginal effects of other variables arereported. Using replication data, we estimate:

conflictit = β1tempit + β2precit + µi + θt + εit (C.5)

where i=grid cell, t=year, µi is a grid fixed effect, and θt is a year fixed effect.conflict, temp and prec are the conflict, precipitation, and temperature variables,respectively, as defined in their paper. Errors account for spatial correlation acrosscontemporaneous grid cells within 100 km of one another and grid-specific serialcorrelation (equivalent to grid-level clustering) following the approach of ref. Hsiang(2010). The coefficient on temperature is large and statistically significant at the95% confidence level (p=0.027), which is at odds with the paper’s conclusions. Theoriginal article does not test for the marginal effect of temperature, and instead onlypresents models that are quadratic in temperature and then separately tests whetherthe coefficients on temp and temp2 are significant, whereas the correct test for theeffect of temperature requires that both coefficients are tested jointly. As our Fig.2F and the author’s Table 1 Model 5 shows, there is no evidence that the relationshipbetween conflict and temperature is quadratic in this sample, so there is no reasonto use a quadratic model.

To demonstrate that the marginal effect of temperature that we report from thepaper is representative of the many different models estimated in the original article,we re-estimate multiple versions of Equation C.5 for both of his outcome variables(“conflict” is a dummy for the “first event of a conflict that generated at least 25deaths in the same year”; “event” is a dummy for whether or not there was a conflictin that cell-year. We label these “onset” and “incidence” in the Figure). FollowingTheisen, we estimate models with climate variables in levels or in anomalies (i.e.subtracting the cell mean and dividing by the cell standard deviation). Finally,because Theisen notes that temperature variables appear to switch signs dependingon how they are lagged, we estimate models with either 0, 1, or 3 lags (e.g. the modelwith 3 lags includes Tempt, Tempt−1, Tempt−2, and Tempt−3). For each model wecalculate the standardized effect of temperature, which for models with lags is thesummed effect of temperature across all lags including the zero lag. Results areshown in Fig. C.2. None of the 12 models estimate can reject our median estimateof 14% per 1σ, and 7 out of 12 models cannot reject a 100% per 1σ effect.


Figure C.2: Standardized effect sizes in Theisen (2012).

% c

hang

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limat

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−100−75−50−25

0255075

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lags

= 3

lags

= 3

lags

= 1

lags

= 1

lags

= 0

**

lags

= 0

lags

= 1

lags

= 1

lags

= 3

lags

= 3

lags

= 0

lags

= 0

Onset Incidence

Each marker represents the estimated effect of a 1σ increase in a climate variable, withthe magnitude of the response expressed as a percentage change in the outcome variable,relative to the mean conflict rate. Whiskers represent the 95% confidence interval on this

point estimate, with standard errors corrected for spatial correlation. Colors are as inFig. 5; circular markers indicate models using climate variables in levels, and triangular

markers indicate models using climate variables in anomalies. Models include the numberof climate lags as indicated on the x-axis, and the estimate marked with “**” – the modelclosest in functional form to the other studies we analyze – is shown in Fig. 5. Outcomesare given at the top of the figure and are as described in the text. The dashed line is the

median estimate from Fig. 5.


• Theisen, Holterman and Buhaug 2012 Theisen, Holtermann, and Buhaug (2011).The published version of this paper does not control for location fixed effects andincludes outcome variables as covariates. Preserving the variable names in their datafiles, we use data from the authors to estimate the following specification:

onsetxit = βspi6dumit + µi + θt + εit (C.6)

where i=grid cell, t=year, and onsetx and spi6dum are the conflict onset and pre-cipitation variables as defined in their paper. We run the specification on the fulldataset instead of downsampling the data as was done in the original analysis. Aswith the other gridded datasets, errors are two-way clustered at the grid level andat the country-year level

The estimated effect of precipitation is positive, but as indicated in the figure theconfidence interval is large, meaning that large negative or positive effects cannot beruled out. We note that this high level of uncertainty is “built in” to the statisticallyunderpowered design of the study, which attempts to predict 59 pixel-by-year con-flict events across 363,811 pixel-by-year observations. The primary innovation of thestudy is to assign large scale wars to very specific locations (∼55km × 55km) thatare assigned pixel-specific levels of water availability. However, an important impactof increasing the resolution of the civil war data is that conflicts become extraordi-narily rare events in the data, with the unconditional probability that any locationexhibits conflict being 59

363,811 = 0.00016 = 0.016%. Because at most only a fractionalcomponent of these conflicts could be attributed to climatic forcing, detecting thisinfluence is difficult or impossible under reasonable assumptions.

Details on select excluded papers

Some quantitative papers in this literature did not meet our criteria. A subset of thesepresent the same data and same fundamental analysis as other included papers, as indicatedbelow.

• Adano et al (J. Peace Res., 2012). We did not include this study because it presentedlargely qualitative analysis and summary statistics. Nonetheless, we note that theauthors appear to show a positive correlation between high precipitation years andcattle raids in Kenya.

• Benjaminsen, Tor, Alinon, Buhaug and Buseth (J. Peace Res., 2012). This arti-cle presents quantitative data but states that it is a qualitative study and not aquantitative study, so it did not fall within the scope of our review.

• Dell 2012 (“Insurgency and long-run development: Lessons from the Mexican Revo-lution”, working paper). We did not include this paper because it does not meet our


standards for including location-specific fixed effects. Dell shows that locations inMexico that experienced severe drought just prior to the Mexican Revolution weresubstantially more likely to participate in the ensuing Revolution. While her droughtmeasure is constructed from local deviations from location-specific means, she can-not similarly demean the dependent variable because there is only one observationper locality (demeaning both the independent and dependent variables is equivalentto including locality-specific fixed effects).

• Gartzke (J. Peace Res., 2012). This study was not included because the area-weighted global average temperature variables are dominated by uninhabited regions,such the oceans and polar regions, and thus do not reflect the conditions of countriesin the sample.

• Koubi, Bernauer, Kalbhenn, and Spilker (J. Peace Res., 2012). The authors do notestimate the reduced form relationship between climate and conflict, but the reducedform that they would have estimated is redundant with Dell, Jones, and Olken Dell,Jones, and Olken (2012b) for the global sample, and Burke et al Burke et al. (2009a)for the African sample. For this reason the study is not included.

• Nel and Righarts (International Studies Quarterly, 2008). This paper finds thatnatural disasters significantly increase the risk of armed conflict, but the paper doesnot use location-specific fixed effects and appears to use disaster and conflict dataidentical to that of Bergholt and Lujala (which we include). For that reason, we donot include this paper.

• Raleigh and Kniveton (J. Peace Res. 2012). This paper was not included becauseit did not meet our standards for including location-specific controls. It is not re-analyzed because it presents the same data as O’Loughlin et al. O’Loughlin et al.(2012) and Harari and La Ferrara 2013 Harari and La Ferrara (2013), which wereanalyzed according to our methodological criteria and are included in the analysis.

• Sletteback (J. Peace Res., 2012). This paper was not included because it did notmeet our standards for including location-specific controls. It was not reanalyzedbecause it presents the same data as Bergholt and Lujala (2012), which was analyzedaccording to our methodological criteria.

C.2 Evaluating and combining effect sizes

The goal of our analysis is to identify studies that estimate the causal relationship of climateon some conflict outcome, and to compare the direction and magnitude of the estimatedeffects across studies. Where possible, this latter goal is accomplished by calculating stan-dardized effects for each study. Given an overarching assumption that all of the studies


are comparable in some general sense, we can summarize the distribution of effect sizes ina number of ways.

A simple but transparent first approach, shown in Fig. 4-5, computes the median acrossstudies and shows that most of the confidence intervals of each individual study overlapsthis value. A benefit of this approach is that it is robust to outliers. A downside to thisapproach is that it ignores much of the available information provided by estimates otherthan the median estimate. Being cognizant of both this benefit and cost, we tabulate me-dian values for all estimates and for temperature-only estimates in Table C.1.

A second approach, also shown in Fig. 4-5, assumes that while not all the studies aremeasuring the same specific outcome, the standardized effects we calculate could describea generic phenomenon that is common across samples. Under this assumption, a commonapproach to summarizing the phenomenon is to compute the weighted average across esti-mates, using inverse-variance weights Hedges and Olkin (1985). For a set of M estimatesindexed by j, each with estimated treatment effect βj and associated standard error σj , aweighted estimate of the mean effect across studies is

β =M∑j=1

ωj βj (C.7)

where ωj is the weight for study j, and∑ωj = 1. The estimated variance of β is

V ar(β) =M∑i=1

M∑j=1

[ωiωjCov(βi, βj)

](C.8)

If the studies are independent, then Cov(βi, βj) = 0 for all i 6= j and

V ar(β) =

M∑j=1

ω2j σj

2 (C.9)

Many of our estimates are likely independent – eg. violence in United States baseballgames is unlikely to be correlated with Hindu-Muslim riots in India. However, otherstudies use common datasets for either climate or conflict variables and/or overlap in theirsample, suggesting their estimated effects might indeed be correlated. Because we have nopractical way to measure the cross-study correlation in parameter estimates, we begin bysimply assuming it is zero (allowing us to use Eq. C.9) and later relax this assumption.

Because of the Central Limit Theorem, it is natural to assume that our βj ’s are eachnormally distributed. Under this assumption, the optimal2 weighting scheme is

ωj =

1σ2j∑M

j=11σ2j

(C.10)

2This approach is considered optimal because it minimizes V ar(β).


where the weight assigned to each estimate is proportional to the inverse of its estimatedvariance. Because the inverse of variance is termed “precision”, this approach is called“precision-weighting” both in the literature and our main text. The term in the denomi-nator is simply the sum of all inverse variances, which is necessary to ensure that the sumof weights equals one. We use the weights from Equation C.10 applied to Equations C.7and C.9 to estimate the precision-weighted mean and confidence interval shown in Fig. 4-5of the main text. These values are also tabulated in Table C.1.

In a third approach, we expand on the precision-weighting approach to more fullycharacterize the distribution of effects a study might obtain, rather than simply focusingon only the precision-weighted mean estimate β. Defining Nβ(m, s) to be a normallydistributed probability density function over values of β centered on m with standarddeviation s, we construct an estimate for the probability distribution Bβ that describes the

probability of obtaining an estimate β unconditional on the study sample:

Bβ =

M∑j=1

ωjNβ(βj , σj) (C.11)

where we continue to use the weights from Equation C.9 so that E[Bβ] = β for consistency.Our estimates of Bβ for all studies and temperature-only studies are shown in Fig. 4-5 ofthe main text (solid lines). Percentiles from these four distributions are also tabulated inTable C.1.

As discussed above, the estimates of β are unlikely to be independent across all studies(Cov(βi, βj) 6= 0 for all i 6= j). We cannot estimate all of these covariances, but we think itis both reasonable and conservative to assume that they are likely to be weakly positive inour setting – as they are probably an increasing function of the spatial and temporal overlapin a given set of studies. To develop a sense of whether our assumption of “no cross-studycorrelation” is generating a false sense of statistical significance in our precision-weightedaverage effects, we assume that all cross-study covariances take on arbitrary positive valuesand ask how this alters our estimates of V ar(β) using Equation C.8. Observing that thepopulation of cross-study estimates have correlation ρij = Cov(βi, βj)/(σiσj), we assumeρij ∈ {0.1, 0.3, 0.5, 0.7} and then estimate

Cov(βi, βj) = ρij σiσj (C.12)

which are then used in Equation C.8. Using these four values for ρij , we obtain estimates

for√V ar(β) of 2.1, 3.1, 3.8, and 4.5, respectively, for the studies of intergroup conflict

(our least-precise result). Since the estimated mean effect is 11.1 for this set of studies,we infer that this result would still be statistically significant even if ρij = 0.7 for all pairsof studies. Since it is very likely that ρij is much lower for all pairs of studies, this shows


Tab

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.1:

Sum

mar

yst

atis

tics

for

the

dis

trib

uti

onof

effec

tsac

ross

studie

s

Med

ian

Mea

n*

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les

ofBβ

2.5%

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%97

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Inte

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up

13.5

611

.12

1.34

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040

.10

Inte

rgro

up

(Tem

p.)

23.9

613

.21

1.95

-4.4

0-1

.30

5.60

9.70

16.6

040

.10

46.0

0In

terp

erso

nal

3.89

2.29

0.12

1.10

1.20

1.50

2.20

2.60

4.00

4.20

Inte

rper

son

al(T

emp

)2.

482.

260.

121.

101.

201.

502.

202.

603.

904.

20

*β,

**Var(β

)


that our central conclusion about the general relationship between climate an conflict isnot dependent on our assumption of cross-study correlations.

Estimating the distribution of effect sizes with a Bayesianhierarchical model

It is likely the case that differences among estimated effect sizes are not due to samplingvariability alone. That is, studies looking at the effect of climate on different outcomesmight be expected to share some similarities (different outcomes might be related), butalso some important differences (some outcomes or samples might exhibit different re-sponses to climate). The precision-weighting averages above are no longer optimal underthese conditions since the sampling variability is not strictly normal (although these re-sults remain useful), and the precision-weighted distribution Bβ – while it does not makeany assumptions about cross-study sampling variability – does not use all the availableinformation.

We use a fourth approach, the Bayesian hierarchical normal model, which provides away to model the distribution of effect sizes while simultaneously allowing for similari-ties and differences across studies. This approach utilizes the available information moreefficiently than our estimate of Bβ and provides more insight into the structure of between-study variation, although it is noteworthy that the unconditional posterior distribution forβ ends up being similar in this setting. Our implementation closely follows Gelman et alGelman et al. (2004), and readers are referred to that volume (particularly Chapter 5) fora more comprehensive treatment.

As before, consider a set of M independent studies, each estimating a treatment effectβj . Denote each study’s estimate of that treatment effect βj , with standard error σj .Further assume that these treatment effects βj are drawn from a normal distribution withunknown mean µ and standard deviation τ . In this setting, it could be the case that βjis the same across studies and observed variation in the βj ’s results from sampling erroralone (implying τ = 0 and βj = µ for all j), or it could be the case that the “true” effect ineach study is different (meaning τ > 0). Because τ is unknown, the goal of this approachis to compute a distribution of τ ’s that are consistent with the observed βj ’s and σj ’s, andthen use these estimates to simulate the distribution of each βj .

Intuitively, if estimated treatment effects in all studies are very near one another andhave relatively wide and overlapping confidence intervals, then most simulated values of τare likely to be close to zero. Alternatively, if there is large variation in the estimated effectsbut each effect is estimated precisely, then τ will � 0 and “true” treatment effects likelydiffer across studies. Casual observation of Fig. 5 perhaps suggests a world somewhere inbetween: substantially overlapping confidence intervals, but also substantial variation inthe estimated effects with some confidence intervals that do not overlap.

Using a uniform prior, we apply Bayes’ Rule to update our estimates of µ, τ and theβi’s for estimates of interpersonal violence and intergroup conflict seperately Gelman et al.


Figure C.3: Conditional posterior means of the study-specific treatmenteffects.

0 2 4 6 8 10

−2

0

2

4

6

8

10

12

tau

0 5 10 15 20 25

−20

−10

0

10

20

30

40

50

tau

% c

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r 1σ

cha

nge

in c

limat

e

% c

hang

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r 1σ

cha

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limat

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Intergroup conflictInterpersonal violence

Conditional posterior means of treatment effects for the 11 interpersonal violence studies(left panel) and the 21 intergroup conflict studies (right panel), as a function of τ , the esti-mated between-study standard deviation. The histograms at bottom shows the distributionsof the estimated τ .

(2004). We then use 10,000 simulations to characterize the posterior distributions of thesevariables and present the results in Fig. C.3 and Tables C.2-C.3. In Fig. C.3, each linein the two panels represents the estimated effect size in a single study, conditional on thebetween-study standard deviation τ . The estimated distribution of τ across the 10,000simulations is shown at the bottom of each panel. For both the intergroup conflict stud-ies and individual conflict studies, simulated values of τ are distributed away from zero,meaning that the estimated treatment effects are very unlikely to describe a single under-lying value and suggesting that there are likely important differences across studies. Giventhe range of outcomes, geographies, and time periods that these studies cover, this is notsurprising. Nonetheless, the component of the effects β that is common across studies (µ)tends to be substantial (median=3.0%/σ for interpersonal violence, median=13.8%/σ forintergroup conflict) and larger than the cross-study standard deviation τ (median=1.4%/σfor interpersonal violence, median=9.0%/σ for intergroup conflict). Thus, while there isstrong evidence of important differences between studies, there is simultaneously strongevidence that there is also something in common between these studies. There remainsconsiderable heterogeneity in the response to climate across studies that should be recog-nized, and understanding the sources of this variation could be a fruitful subject for future


Table C.2: Posterior quantiles of treatment effects for the 10 studies on interpersonalviolence.

Posterior distribution

# Study year βj σj 2.5% 25% median 75% 97.5%

1 Ranson 2012 1.47 0.45 0.77 1.33 1.64 1.93 2.502 Jacob Lefgren Moretti 2007 1.55 0.20 1.20 1.46 1.59 1.72 1.983 Card and Dahl 2011 2.18 1.17 0.66 1.90 2.52 3.11 4.344 Ranson 2012 2.42 0.30 1.87 2.25 2.45 2.64 3.005 Jacob Lefgren Moretti 2007 2.54 0.23 2.12 2.40 2.55 2.70 2.996 Ranson 2012 3.89 0.35 3.13 3.59 3.82 4.06 4.527 Larrick et al 2011 4.32 1.42 1.69 2.93 3.63 4.40 5.998 Sekhri and Storeygard 2012 5.43 1.74 1.74 3.09 3.90 4.87 6.939 Sekhri and Storeygard 2012 7.51 2.17 1.90 3.36 4.33 5.53 8.1910 Auliciems and DiBartolo 1995 16.28 5.74 1.01 2.77 3.79 5.16 9.4711 Miguel 2005 21.45 14.45 0.01 2.20 3.16 4.34 8.23

Mean, µ 1.94 2.64 3.02 3.49 4.84Standard deviation, τ 0.62 1.05 1.43 1.98 3.77

Predicted effect, β∗j 1.05 2.08 2.78 3.91 6.84

Estimates are based on 10,000 simulation draws from a Bayesian hierarchical model. The βj andσj columns represent our original estimated effect and standard error from each study. The lastthree rows give the posterior distributions for the population parameters µ and τ , as well as the“predicted effect” β∗j (the predicted outcome of a new study).

inquiry.An additional insight provided by this approach is that it allows us to formally consider

the plausibility of point estimates reported by individual studies, given what we learn fromall the other studies. Our simulations estimate the distribution of individual βj ’s, given

the individual estimates of βj , σj and the distributions of µ and τ , which encapsulateinformation about the full collection of results. In cases where the uncertainty in estimatesis large, our simulations rely more heavily on information about the group of studies (µ),since the study-specific information (βj) is less likely to be reliable3. We describe theseposterior distributions for each study in Tables C.2-C.3. In situations where the estimatedeffect βj is far out in the tail of the posterior distribution for that parameter, the immediateimplication is that either those point estimates are unlikely to be accurate or that thereis something unique about that study that sets it apart from the rest of the literature forsome substantive, albeit not yet well understood, reason.

3This effect results in “shrinkage” in the posterior distribution of βj ’s towards the group meanGelman et al. (2004).

APPENDIX C. CLIMATE AND CONFLICT APPENDIX 197T

able

C.3

:P

oste

rior

quan

tile

sof

trea

tmen

teff

ects

for

the

21st

udie

son

inte

rgro

up

conflic

t.

Pos

teri

ord

istr

ibu

tion

#S

tud

yye

arβj

σj

2.5%

25%

med

ian

75%

97.5

%

1T

hei

sen

Hol

term

ann

Bu

hau

g20

11-1

2.54

15.5

3-1

1.92

1.61

7.72

12.6

522

.69

2B

ergh

olt

and

Lu

jala

2012

-3.6

84.

83-8

.62

-2.3

50.

964.

3010

.36

3B

uh

au

g20

101.

096.

17-5

.59

1.97

5.68

9.26

15.4

74

Del

lJon

esO

lken

2012

6.21

10.4

4-3

.72

6.19

10.7

615

.17

24.6

85

Bu

rke

2012

7.20

3.82

1.44

6.06

8.45

10.8

615

.25

6H

ara

rian

dL

aF

erra

ra20

118.

913.

802.

957.

499.

8312

.06

16.3

47

Fje

lde

an

dvon

Uex

ku

ll20

129.

415.

491.

347.

5410

.63

13.6

619

.94

8M

igu

elS

aty

anat

hS

erge

nti

2004

9.74

4.14

3.33

8.07

10.6

013

.03

17.7

59

Hid

alg

oet

al

2010

12.2

92.

967.

0210

.49

12.3

614

.19

17.8

310

Lev

yet

al

2005

13.3

38.

111.

689.

4613

.27

17.2

825

.37

11

Bu

rke

etal

2009

13.5

66.

683.

039.

9813

.34

17.0

224

.31

12

Hen

dri

xan

dS

aleh

yan

2012

13.9

46.

124.

1010

.36

13.6

117

.06

23.9

013

Hsi

an

gM

eng

Can

e20

1117

.11

6.92

4.94

11.8

215

.56

19.4

127

.22

14

Bu

rke

and

Lei

gh20

1030

.81

14.3

33.

8012

.76

18.0

423

.83

37.5

115

Cou

tten

ier

an

dS

oub

eyra

n20

1231

.34

9.31

8.77

16.5

321

.59

27.0

438

.16

16

O’L

augh

lin

etal

2012

31.6

39.

299.

2116

.68

21.8

027

.07

38.0

617

May

stad

tE

cker

Mab

iso

2013

35.8

49.

4310

.03

18.1

823

.59

29.0

040

.41

18

Del

lJon

esO

lken

2012

42.1

912

.18

8.74

17.1

623

.17

29.8

943

.15

19

Boh

lken

and

Ser

genti

2011

50.3

730

.74

-0.2

710

.67

16.3

023

.08

39.8

720

Th

eise

n20

1275

.91

36.9

0-0

.36

11.0

816

.85

23.7

942

.49

21

Bru

ckn

eran

dC

icco

ne

2010

95.3

850

.62

-1.7

510

.39

15.8

322

.56

40.5

4

Mea

n,µ

8.74

11.9

713

.82

16.0

120

.93

Sta

nd

ard

dev

iati

on,τ

2.96

6.83

9.00

11.3

217

.17

Pre

dic

ted

effec

t,β∗ j

-2.7

08.

3812

.95

19.0

434

.98

Est

imat

esar

eb

ased

on10

,000

sim

ula

tion

dra

ws

from

aB

ayes

ian

hie

rarc

hic

al

mod

el.

Th

eβj

an

dσj

colu

mn

sre

pre

sent

ou

ror

igin

ales

tim

ated

effec

tan

dst

and

ard

erro

rfr

omea

chst

ud

y.T

he

last

thre

ero

ws

giv

eth

ep

ost

erio

rd

istr

ibu

tion

sfo

rth

ep

opu

lati

onp

aram

eter

sµ

andτ,

asw

ell

asth

e“p

red

icte

deff

ect”β∗ j

(th

ep

red

icte

dou

tcom

eof

an

ewst

ud

y).


C.3 Publication bias

Following Card and Krueger Card and Krueger (1995) and Disdier and Head Disdier andHead (2008), standard sampling theory suggests that the t-stat on a coefficient estimateshould be proportional to the degrees of freedom in the study. In particular, with the nullhypothesis H0 = 0, independent variable X, errors e, n− k degrees of freedom, and againindexing studies by j:

t(βj) =βjσj

=βj( √e′jej√

nj−kj√X′jXj

) =√nj − kj ×

βj√X ′jXj√e′jej

(C.13)

Taking logs, we see that there should be unit elasticity between the log of the t-stat and thelog of the square root of the degrees of freedom. We use this insight to look for evidenceof publication bias in the literature we analyze Card and Krueger (1995); Disdier andHead (2008). If there is a true relationship between climate and human conflict, than weexpect the statistical power of studies to increase with their sample size (and thus withtheir degrees of freedom). However, if there is no true relationship, and instead authorsare just searching through data until they find data that allows them to reject H0 usingstandard tests, then large sample sizes should provide no benefit in terms of statisticalpower. Thus, if publication bias is a major problem in this literature, we predict thatlog(t-stat) should not rise with log(

√n− k). For example, in Card and Krueger, the

authors found a negative relationship between t-stats and degrees of freedom, which theyinterpreted as strong evidence of publication bias.

Fig. C.4 shows the plotted relationship between the log of the t-statistic and the log ofthe square root of the degrees of freedom, for the 32 studies for which we are able to calculatestandardized effects (we use author-reported statistics here because those are the valuesthat authors, editors and reviewers would consider at the time of release/publication). Theunit elasticity is given by the 45-degree line, and OLS estimates of the relationship for thefull sample and for the temperature-focused studies are given by the dashed lines. Westrongly reject a slope of zero (see Columns 1-2 in Table C.4). And although we can rejecta 1-to-1 relationship, studies with larger sample sizes do have larger t-statistics in theclimate and conflict literature we survey, suggesting that authors with large samples arenot simply searching through specifications or data mining to find marginally significanteffects. We note that for both samples, the upward relationship stands in sharp contrastto the results in Card and Krueger, with the negative slope they estimate. Our estimatesare more similar to that of Disdier and Head (2009), who interpret their results as rulingout any large role for publication bias in the trade literature that they survey.

Card et al Card, Kluve, and Weber (2010) argue that there is an important reasonwhy the slope coefficient that we focus on could be less than one even in the absence ofpublication bias, namely, if studies with larger samples also employ more complex researchdesigns, altering the study’s “design effect”. To the extent that this is true, we would


Figure C.4: Relationship between log of t-stat and log of the square rootof the degrees-of-freedom

0 2 4 6 8

0

2

4

6

8

log sqrt degrees of freedom

log

t−st

at

OLS (all) = 0.38

OLS (temp) = 0.45

Author reported t-statistics. Circles represent studies focusing on rainfall, triangles studiesfocusing on temperature.


Table C.4: The relationship between log t-stat and log square root of the degrees-of-freedom, using author-reported t-statistics.

(1) (2)Full Temp

log sqrt deg. of. freedom 0.380∗∗∗ 0.454∗∗

(0.123) (0.180)Constant -0.686 -0.987

(0.585) (0.907)Observations 32 20R squared 0.242 0.260P-val elasticity = 1 0.000 0.007

Standard errors in parentheses∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01

Column 1 is the full sample, Column 2 the studies that focus on temperature. The bottom row isthe p-value on the test that the d.o.f. coefficient is unity.

expect a slope coefficient less than one, but it ultimately becomes difficult to quantify theprecise extent of publication bias in this case. Card et al Card, Kluve, and Weber (2010)cannot reject a zero slope for the vast labor economics literature they survey on the impactsof active labor market policies, but they conclude that there is unlikely to be considerablepublication bias in that setting due to their point on research design complexity.

Nevertheless, to help prevent publication biases from developing in this field, we brieflyoutline the evidence needed to establish a compelling null result in a specific context – sothat researchers, editors and reviewers may be confident in a strong null finding shouldthey encounter one. To demonstrate that climatic variables have no effect on humanconflict, studies must (i) account for unobservable differences between populations Holland(1986); Angrist and Pischke (2008) and trends in conflict Hsiang and Burke (in press); (ii)document that both linear models and non-linear models exhibit no association; (iii) controlfor all relevant climatological covariates and their lags simultaneously Auffhammer et al.(2013b); (iv) stratify their sample using baseline climate conditions; (v) avoid controlling forsocio-economic covariates that are also influenced by climatic variables Angrist and Pischke(2008); (vi) demonstrate that their confidence interval excludes substantial effect sizesHsiang and Burke (in press) reported elsewhere, such as our median estimates presentedhere; (vii) use simple simulations to demonstrate that their statistical tests are adequatelypowered.


C.4 Projected changes in temperature

In Fig. 6 we plot expected warming by 2050, calculated as the mean projected warmingat a given location divided by the historical standard deviation of annual temperatureat that location. The projected warming at each location is the mean at that locationcomputed across the 21 available global climate models running the A1B emissions scenario.The historical standard deviation of temperature at each location is calculated using half-degree gridded weather data from the University of Delaware dataset. Almost all inhabitedlocations warm by > 2σ, with the largest increases exceeding 4σ in tropical regions thatare already warm and currently experience very low inter-annual temperature variability.

Climate and the productivity, health, and peacefulness of society · 2018. 10. 10. · 1 Abstract...

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