Goldilocks RCTs

What better way to ring in the new year than to announce that Louis Preonas, Matt Woerman, and I have posted a new working paper, "Panel Data and Experimental Design"?  The online appendix is here (warning - it's math heavy!), and we've got a software package, called pcpanel, available for Stata via ssc, with the R version to follow.*

TL;DR: Existing methods for performing power calculations with panel data only allow for very limited types of serial correlation, and will result in improperly powered experiments in real-world settings. We've got new methods (and software) for choosing sample sizes in panel data settings that properly account for arbitrary within-unit serial correlation, and yield properly powered experiments in simulated and real data. 

The basic idea here is that researchers should aim to have appropriately-sized ("Goldilocks") experiments: too many participants, and your study is more expensive than it should be; too few, and you won't be able to statistically distinguish a true treatment effect from zero effect. It turns out that doing this right gets complicated in panel data settings, where you observe the same individual multiple times over the study. Intuitively, applied econometricians know that we have to cluster our standard errors to handle arbitrary within-unit correlation over time in panel data settings.** This will (in general) make our standard errors larger, and so we need to account for this ex ante, generally by increasing our sample sizes, when we design experiments. The existing methods for choosing sample sizes in panel data experiments only allow for very limited types of serial correlation, and require strong assumptions that are unlikely to be satisfied in most panel data settings. In this paper, we develop new methods for power calculations that accommodate the panel data settings that researchers typically encounter. In particular, we allow for arbitrary within-unit serial correlation, allowing researchers to design appropriately powered (read: correctly sized) experiments, even when using data with complex correlation structures. 

I prefer pretty pictures to words, so let's illustrate that. The existing methods for power calculations in panel data only allow for serial correlation that can be fully described with fixed effects - that is, once you put a unit fixed effect into your model, your errors are no longer serially correlated, like this:

But we often think that real panel data exhibits more complex types of serial correlation - things like this:

Okay, that's a pretty stylized example - but we usually think of panel data being correlated over time - electricity consumption data, for instance, generally follows some kind of sinusoidal pattern; maize prices in East Africa at a given market typically exhibit correlation over time that can't just be described with a level shift; etc; etc; etc. And of course, in the real world, data are never nice enough that including a unit fixed effect can completely account for the correlation structure.

So what happens if I use the existing methods when I've got this type of data structure? I can get the answer wildly wrong. In the figure below, we've generated some difference-in-difference type data (with a treatment group that sees treatment turn on halfway through the dataset, and a control group that never experiences treatment) with a simple AR(1) process, calculated what the existing methods imply the minimum detectable effect (MDE) of the experiment should be, and simulated 10,000 "experiments" using this treatment effect size. To do this, we implement a simple difference-in-difference regression model. Because of the way we've designed this setup, if the assumptions of the model are correct, every line on the left panel (which shows realized power, or the fraction of these experiments where we reject the null of no treatment) should be at 0.8. Every line on the right panel should be at 0.05 - this shows the realized false rejection rate, or what happens when we apply a treatment effect size of 0. 

Adapted from Figure 2 of Burlig, Preonas, Woerman (2017). The y-axis of the left panel shows the realized power, or fraction of the simulated "experiments" described above that reject the (false) null hypothesis; the y-axis of the right panel shows the realized false rejection rate, or fraction of simulated "experiments" that reject the true null under a zero treatment effect. The y-axis in both plots is the number of pre- and post-treatment periods in the "experiment." The colors show increasing levels of AR(1) correlation. If the Frison and Pocock model were performing properly, we should expect all of the lines on the left panel to be at 0.80, and all of the lines in the right panel to be at 0.05. Because we're clustering our standard errors in this setup, the right panel is getting things right - but the left panel is wildly off, because the FP model doesn't account for serial correlation. 

We're clustering our standard errors, so as expected, our false rejection rate is always right at 0.05. But we're overpowered in short panels, and wildly underpowered in longer ones. The easiest way to think about statistical power is that if you aimed to be powered at 80% (generally the accepted standard, and meaning that you'll fail to reject a false null 20% of the time), you're going to fail to reject the null - even when there is a true treatment effect - 20% of the time. So that means if you end up powered to, say, 20%, as happens with some of these simulations, you're going to fail to reject the (false) null 80% of the time. Yikes! What's happening here is essentially that by not taking serial correlation into account, in long panels, we think we can detect a smaller effect than we actually can. Because we're clustering our standard errors, though, our false rejection rate is disciplined - so we get stars on our estimates way less often than we were expecting.***

By contrast, when we apply our "serial-correlation-robust" method, which takes the serial correlation into account ex ante, this happens:

Adapted from Figure 2 of Burlig, Preonas, Woerman (2017). Same y- and x-axes as above, but now we're able to design appropriately-powered experiments for all levels of AR(1) correlation and all panel lengths - and we're still clustering our standard errors, so the false rejection rates are still right. Whoo!

That is, we get right on 80% power and 5% false rejection rates, regardless of the panel length and strength of the AR(1) parameter. This is the central result of the paper. Slightly more formally, our method starts with the existing power calculation formula, and extends it by adding three terms that we show are sufficient to characterize the full covariance structure of the data (see Equation (8) in the paper for more details).

If you're an economist (and, given that you've read this far, you probably are), you've got a healthy (?) level of skepticism. To demonstrate that we haven't just cooked this up by simulating our own data, we do the same thought experiment, but this time, using data from an actual RCT that took place in China (thanks, QJE open data policy!), where we don't know the underlying correlation structure. To be clear, what we're doing here is taking the pre-experimental period from the actual experimental data, and calculating the minimum detectable effect size for this data using the FP model, and again using our model.**** This is just like what we did above, except this time, we don't know the correlation structure. We non-parametrically estimate the parameters that both models need in order to calculate the minimum detectable effect. The idea here is to put ourselves in the shoes of real researchers, who have some pre-existing data, but don't actually know the underlying process that generated their data. So what happens?

The dot-dashed line shows the results when we use the existing methods; the dashed line shows the results when we guess that the correlation structure is AR(1); and the solid navy line shows the results using our method. 

Adapted from Figure 3 of Burlig, Preonas, Woerman (2017). The axes are the same as above. The dot-dashed line shows the realized power, over varying panel lengths, of simulated experiments using the Bloom et al (2015) data in conjunction with the Frison and Pocock model. The dashed line instead assumes that the correlation structure in the data is AR(1), and calibrates our model under this assumption. Neither of these two methods performs particularly well - with 10 pre and 10 post periods, the FP model yields experiments that are powered to ~45 percent. While the AR(1) model performs better, it is still far off from the desired 80% power. In contrast, the solid navy line shows our serial-correlation-robust approach, demonstrating that even when we don't know the true correlation structure in the data, our model performs well, and delivers the expected 80% power across the full range of panel lengths. 

Again, only our method achieves the desired 80% power across all panel lengths. While an AR(1) assumption gets closer than the existing method, it's still pretty off, highlighting the importance of thinking through the whole covariance structure.

In the remainder of the paper, we A) show that a similar result holds using high-frequency electricity consumption data from the US; B) show that collapsing your data to two periods won't solve all of your problems; C) think through what happens when using ANCOVA (common in economics RCTs) -- there are some efficiency gains, but much fewer than you'd think if you ignored the serial correlation; and D) couch these power calculations in a budget constrained setup to think about the trade-offs between more time periods and more units. *wipes brow*

A few last practical considerations that are worth addressing here:

• All of the main results in the paper (and, indeed, in existing work on power calculations) are designed for the case where you know the true parameters governing the data generating process. In the appendix, we prove that (with small correction factors) you can also use estimates of these parameters to get to the right answer.
• People are often worried enough about estimating the one parameter that the old formulas needed, let alone the four that our formula requires. While we don't have a perfect answer for this (more data is always better), simply ignoring these additional 3 parameters implicitly assumes they're zero, which is likely wrong. The paper and the appendix provide some thoughts on dealing with insufficient data.
• Estimating these parameters can be complicated...so we've provided software that does it for you!
• We'd also like to put in a plug for doing power calculations by simulation when you've got representative data - this makes it much easier to vary your model, assumptions on standard errors, etc, etc, etc.  

Phew - managed to get through an entire blog post about econometrics without any equations! You're welcome. Overall, we're excited to have this paper out in the world - and looking forward to seeing an increasing number of (well-powered) panel RCTs start to hit the econ literature!

* We've debugged the software quite a bit in house, but there are likely still bugs. Let us know if you find something that isn't working!

** Yes, even in experiments. Though Chris Blattman is (of course) right that you don't need to cluster your standard errors in a unit-level randomization in the cross-section, this is no longer true in the panel. See the appendix for proofs.

*** What's going on with the short panels? Short panels will be overpowered in the AR(1) setup, because a difference-in-differences design is identified off of the comparison between treatment and control in the post-period vs this same difference in the pre-period. In short panels, more serial correlation means that it's actually easier to identify the "jump" at the point of treatment. In longer panels, this is swamped by the fact that each observation is now "worth less". See Equation (9) of the paper for more details.

**** We're not actually saying anything about what the authors should have done - we have no idea what they actually did! They find statistically significant results at the end of the day, suggesting that they did something right with respect to power calculations, but we remain agnostic about this. 

Full disclosure: funding for this research was provided by the Berkeley Initiative for Transparency in the Social Sciences, a program of the Center for Effective Global Action (CEGA), with support from the Laura and John Arnold Foundation.

Is the file drawer too large? Standard Errors in Stata Strike Back

We've all got one - a "file drawer" of project ideas that we got a little way into and abandoned, never to see the light of day. Killing projects without telling anybody about it is bad for science - both because it likely leads to duplicate work, and because it makes it hard to know how much we should trust published findings. Are the papers that end up in journals just the lucky 5%? Do green jelly beans really cause cancer if a journal tells me so?!

I suspect that lots of projects die as a result of t < 1.96. It's hard to publish or get a job with results that aren't statistically significant, so if a simple test of a main hypothesis doesn't come up with stars, chances are that project ends up tabled (cabineted? drawered and quartered?). 

But what if too many papers are ending up in the file drawer? Let's set aside broader issues surrounding publishing statistically insignificant results - it turns out that Stata* might be contributing to our file drawer problem. Or, rather, Stata who don't know exactly what their fancy software is doing. Watch out - things are about to get a little bit technical.

Thanks to a super influential paper, Bertrand, Duflo, and Mullainathan (2004), whenever applied microeconometricians like me have multiple observations per individual, we're terrified that OLS standard errors will be biased towards zero. To deal with this problem, we generally cluster our standard errors. Great - standard errors get bigger, problem solved, right?

Turns out that's not quite the end of the story. Little-known - but very important! - fact: in short panels (like two-period diff-in-diffs!), clustered standard errors require a small-sample correction. With few observations per cluster, you should be just using the variance of the within-estimator to calculate standard errors, rather than the full variance. Failing to apply this correction can dramatically inflate standard errors - and turn a file-drawer-robust t-statistic of 1.96 into a t-statistic of, say 1.36. Back to the drawing board.**  Are you running through a mental list of all the diff-in-diffs you've run recently and sweating yet? 

Here's where knowing what happens under the hood of your favorite regression command is super important.  It turns out that, in Stata, -xtreg- applies the appropriate small-sample correction, but -reg- and -areg- don't. Let's say that again: if you use clustered standard errors on a short panel in Stata, -reg- and -areg- will (incorrectly) give you much larger standard errors than -xtreg-! Let that sink in for a second. -reghdfe-, a user-written command for Stata that runs high-dimensional fixed effects models in a computationally-efficient way, also gets this right. (Digression: it's great. I use it almost exclusively for regressions in Stata these days.)

Edited to add: The difference between what -areg- and what -xtreg- are doing is that -areg- is counting all of the fixed effects against the regression's degrees of freedom, whereas -xtreg- is not. But in situations where fixed effects are nested within clusters, which is usually true in diff-in-diff settings, clustering already accounts for this, so you don't need to include these fixed effects in your DoF calculation. This would be akin to "double-counting" these fixed effects, so -xtreg- is doing the right thing. See pp. 17--18 of Cameron and Miller (ungated), Gormley and Matsa, Hanson and Sunderam, this Statalist post, and the -reghdfe- FAQ, many of which also cite Wooldridge (2010) on this topic. I finally convinced myself this was real with a little simulation, posted below, showing that if you apply a placebo treatment, -xtreg- will commit a Type I error the expected 5% of the time, but -areg- will do so only 0.5% of the time, suggesting that it's being overly conservative relative to what we'd expect it to do. 

So: spread the Good News - if you've been using clustered standard errors with -reg- or -areg- on a short panel, you should switch to -xtreg- or -reghdfe-, and for once have correctly smaller standard errors. If for whatever reason you're unwilling to make the switch, you can multiply your -reg- or -areg- standard error by 1/sqrt((N-1)/(N-J-1)), where N is the total number of observations in your dataset, and J is the number of panel units (individuals) in your data, and you'll get the right answer again.***

Adjust your do files, shrink your standard errors, empty out your file drawer. Happy end of summer, y'all.

*For the smug R users among us (you know who you are), note that felm doesn't apply this correction either. Edited to add: Also, if you're an felm user, it turns out that felm uses the wrong degrees of freedom to calculate its p-value with clustered standard errors. If you have a large number of clusters, this won't matter, since the t distribution converges decently quickly, but in smaller samples, this can make a difference. Use the exactDOF option to set your degrees of freedom equal to the number of clusters to fix this problem.

**Note: I'm not advocating throwing away results with t=1.36. That would be Bad Science.

*** What about cross-sectional data? When is -areg- right? For more details, please scroll (all the way) down below to read David Drukker's comment on when -areg- is appropriate. Here's a small piece of his comment:

“Sometimes I have cross-sectional data and I want to condition on a
state-level fixed effects. (If I add more individuals to the sample, the
number of fixed effects does not change.) Sometimes I have a short panel and
I want to condition on individual-level fixed effects. (Every new
individual in the sample adds a fixed effect on which I must condition.)”

That is: -areg- is appropriate in the first case, -xtreg- is appropriate in the latter case. All of this highlights for me the importance of understanding what your favorite statistical package is doing, and why it's doing it. Read the help documentation, code up simulations, and figure out what's going on under the hood before blindly running regressions. 

H/t to my applied-econometrician-partners in crime for helping me to do just that.

See also: More Stata standard error hijinks.

Simple example code for Stata -- notice that t goes from 1.39 to 1.97 when we switch from the incorrect to the correct clustered standard errors! Edited to add: The first chunk of code just demonstrates that the SE's are different for different approaches. The second chunk of code runs a simulation that applies a placebo treatment. I wrote it quickly. It's not super computationally efficient.

*************************************************************************
***** IS THE FILE DRAWER TOO LARGE? -- SETUP
*************************************************************************

clear all
version 14
set more off
set matsize 10000
set seed 12345

* generate 100 obs
set obs 1000
* create unit ids
gen ind = _n

* create unit fixed effects
gen u_i = rnormal(1, 10)
* and 2 time periods per unit
expand 2
bysort ind: gen post = _n - 1

* generate a time effect 
gen nu_t = rnormal(3, 5)
replace nu_t = nu_t[1]
replace nu_t = rnormal(3,5) if post == 1
replace nu_t = nu_t[2] if post == 1

* ``randomize'' half into treatment
gen trtgroup = 0
replace trtgroup = 1 if ind > 500

* and treat units in the post-period only
gen treatment = 0
replace treatment = 1 if trtgroup == 1 & post == 1 

* generate a random error
gen eps = rnormal()

**** DGP ****
gen y = 3 + 0.15*treatment + u_i + nu_t + eps

*************************************************************************
***** IS THE FILE DRAWER TOO LARGE? -- ESTIMATION RESULTS
*************************************************************************
*** ESTIMATE USING -reg-

* might want to comment this out if your computer is short on memory

reg y treatment i.post i.ind, vce(cluster ind)
/*

Linear regression Number of obs =2,000
F(1, 999) =.
Prob > F=.
R-squared = 0.9957
Root MSE= 1.0126

(Std. Err. adjusted for 1,000 clusters in ind)
------------------------------------------------------------------------------
 | Robust
 y |Coef. Std. Err.tP>|t| [95% Conf. Interval]
-------------+----------------------------------------------------------------
 treatment | .1782595 .1281184 1.39 0.164-.0731525.4296715
*/

*** ESTIMATE USING -areg-

areg y treatment i.post, a(ind) vce(cluster ind)
/*

Linear regression, absorbing indicators Number of obs =2,000
F( 2,999) =6284.86
Prob > F= 0.0000
R-squared = 0.9957
Adj R-squared = 0.9913
Root MSE= 1.0126

(Std. Err. adjusted for 1,000 clusters in ind)
------------------------------------------------------------------------------
 | Robust
 y |Coef. Std. Err.tP>|t| [95% Conf. Interval]
-------------+----------------------------------------------------------------
 treatment | .1782595 .1281184 1.39 0.164-.0731525.4296715

*/
*** ESTIMATE USING -xtreg-
xtset ind post
xtreg y treatment i.post,fe vce(cluster ind)
/*

Fixed-effects (within) regression Number of obs =2,000
Group variable: ind Number of groups=1,000

R-sq: Obs per group:
 within= 0.9618 min =2
 between = 0.0010 avg =2.0
 overall = 0.1091 max =2

F(2,999)= 12576.01
corr(u_i, Xb)= -0.0004Prob > F= 0.0000

(Std. Err. adjusted for 1,000 clusters in ind)
------------------------------------------------------------------------------
 | Robust
 y |Coef. Std. Err.tP>|t| [95% Conf. Interval]
-------------+----------------------------------------------------------------
 treatment | .1782595 .0905707 1.97 0.049 .0005289.3559901
*/

*** ESTIMATE USING -reghdfe-

reghdfe y treatment, a(ind post) vce(cluster ind)
/*
HDFE Linear regressionNumber of obs =2,000
Absorbing 2 HDFE groups F( 1,999) = 3.88
Statistics robust to heteroskedasticity Prob > F= 0.0493
R-squared = 0.9957
Adj R-squared = 0.9913
Within R-sq.= 0.0039
Number of clusters (ind) =1,000 Root MSE= 1.0126

(Std. Err. adjusted for 1,000 clusters in ind)
------------------------------------------------------------------------------
 | Robust
 y |Coef. Std. Err.tP>|t| [95% Conf. Interval]
-------------+----------------------------------------------------------------
 treatment | .1782595.090548 1.97 0.049 .0005734.3559457
------------------------------------------------------------------------------
*/

*************************************************************************
***** IS THE FILE DRAWER TOO LARGE? -- SIMULATIONS
*************************************************************************

clear all
version 14
set more off
set seed 12345

local nsims = 10000
** set up dataset to save results **
set obs `nsims'
gen pval_areg = .
gen pval_xtreg = .
save "/Users/fburlig/Desktop/file_drawer_sims_out.dta", replace

*** SIMULATION
** NOTE: THIS IS NOT A SUPER EFFICIENT LOOP. IT'S SLOW. 
** YOU MAY WANT TO ADJUST THE NUMBER OF SIMS DOWN.
clear 
forvalues i = 1/`nsims' {
clear
* generate 1000 obs
set obs 1000
* create unit ids
gen ind = _n

* create unit fixed effects
gen u_i = rnormal(1, 10)
* randomize units into treatment
gen randomizer = runiform()

* ``randomize'' half into treatment
gen trtgroup = 0
replace trtgroup = 1 if randomizer > 0.5
drop randomizer

* and 2 time periods per unit
expand 2
bysort ind: gen post = _n - 1

* generate a time effect 
gen nu_t = rnormal(3, 5)
replace nu_t = nu_t[1]
replace nu_t = rnormal(3,5) if post == 1
replace nu_t = nu_t[2] if post == 1

* and treat units in the post-period only
gen treatment = 0
replace treatment = 1 if trtgroup == 1 & post == 1 

* generate a random error
gen eps = rnormal()

**** XTSET
xtset ind post

**** DGP:TREATMENT EFFECT OF ZERO ****
gen y = 3 + 0*treatment + u_i + nu_t + eps

*** store p-value -- -areg-
areg y treatment i.post, absorb(ind) vce(cluster ind)
local pval_areg =2*ttail(e(df_r), abs(_b[treatment]/_se[treatment]))
di `pval_areg'

*** store p-value -- -xtreg-
xtreg y treatment i.post, fe vce(cluster ind)
local pval_xtreg =2*ttail(e(df_r), abs(_b[treatment]/_se[treatment]))
di `pval_xtreg'

use"/Users/fburlig/Desktop/file_drawer_sims_out.dta", clear
replace pval_areg = `pval_areg' in `i'
replace pval_xtreg = `pval_xtreg' in `i'
save "/Users/fburlig/Desktop/file_drawer_sims_out.dta", replace
}

*** COMPUTE TYPE I ERROR RATES
use"/Users/fburlig/Desktop/file_drawer_sims_out.dta", clear

gen rej_xtreg = 0
replace rej_xtreg = 1 if pval_xtreg < 0.05

gen rej_areg = 0
replace rej_areg = 1 if pval_areg < 0.05

sum rej_xtreg
/*
Variable |ObsMeanStd. Dev. MinMax
-------------+---------------------------------------------------------
 rej_xtreg | 10,000 .0501.218162201

*/

sum rej_areg
/*

Variable |ObsMeanStd. Dev. MinMax
-------------+---------------------------------------------------------
rej_areg | 10,000 .0052.071926901
*/

*** NOTE: xtreg commits a type I error 5% of the time
** areg does so 0.5% of the time!

New resource: Intro to econometrics in R

I've added a new resource to this site - all of my section materials from ARE 212, Max Auffhammer's first-year PhD econometrics course, which build off of notes written by Dan Hammer, Patrick Baylis, and Kenny Bell.

These section notes simultaneously provide a gentle introduction to econometrics and to R. I covered very basic coding, including matrix operations and functions; partitioned regression and goodness of fit; hypothesis testing; ggplot2; generalized least squares and maximum likelihood; large sample properties of OLS; non-standard standard errors (twice!); instrumental variables; power calculations; spatial data; and replication, with a bonus intro to Monte Carlo simulation. Quite a full semester! 

It's so nice when everything is well behaved! OLS is even consistent!

I hope these will be a helpful resource to others. A warning: I made many of the materials from scratch and/or expanded existing notes, so there are almost certainly errors. Please let me know if you find any. A more important warning: These notes are rife with bad jokes. Prepare yourselves.

Finally, I owe a debt of gratitude to all of the ARE-212-ers of 2016, who braved 8 AM section (not my choice) and have already dramatically improved these materials. Thanks for being a super fun class!

An end-of-semester gift from one of my students (did I mention I had a great class?) and excellent in-joke for those in the know.

WWP: Forests without borders?

As the semester winds to a close, I've been trying to get back into a better habit of reading new papers. Really, I'm just looking for more excuses to hang out at my local Blue Bottle coffee shop - great lighting, tasty snacks, wonderful caffeine, homegrown in Oakland...what more could I ask for? Sometimes doing lots of reading can feel like a slog - but this week, I stumbled across a really cool new working paper that's well worth a look. The paper, by Robin Burgess, Francisco Costa, and Ben Olken, is called "The Power of the State: National Borders and the Deforestation of the Amazon." Deforestation is a pretty big problem in the Amazon, especially when we think that (on top of the idea that we might want to be careful to protect exhaustible natural resources for their own sake, and not pave paradise to build a parking lot) tropical forests have a large role to play in combating climate change, because trees serve as a pretty darn effective carbon sink. Plus they produce oxygen. Win-win! Despite these benefits, trees are also lucrative, and there are also economic benefits to converting forests into farmland. This has led to a spate of deforestation. 

To combat the destruction of the Amazon, Brazil enacted a series of anti-deforestation policies in 2005-06. It's important to understand whether these policies worked, and it's not obvious ex ante that they would: according to evidence from a friend (and badass spatial data guru/data scientist), Dan Hammer, a deforestation moratorium in Indonesia was unsuccessful: if anything, it led to an increased rate of deforestation. Oops. 

The key figure from Dan's paper. The grey bars indicate times when the Indonesian deforestation moratorium was in effect. The teal line is the deforestation rate in Malaysia, and the salmon line is the rate in Indonesia. Not much evidence here that Indonesia's deforestation rate decreased relative to Malayasia during (after) the gray periods.

The big challenging with studying deforestation, especially when it's been made illegal, is that it's tough to get data on. Going out and counting trees requires a huge effort, and people don't usually like to self-report illegal activity. Like Dan before them, Burgess, Costa, and Olken (hereafter BCO) turn to satellite imagery. As I've said before, I'm excited about the advances in remote sensing - there's an explosion of data, which can be harnessed to measure all kinds of things where we don't necessarily have good surveys (Marshall Burke, ahead of the curve as usual). BCO use 30 x 30 meter resolution data on forest cover from a paper published in Science - ahh, interdisciplinary (and a win for open data!).

Of course, it's not enough to just have a measurement of forest cover - in order to figure out the causal effect of Brazil's deforestation policies, the authors also need an identification strategy. Maybe this is because I've got regression discontinuities on the brain lately, but I think what BCO do is super cool. They use the border between Brazil and its neighbors in the Amazon to identify the effects of Brazil's policy. The argument is that, other than the deforestation policies in the different countries, parts of the Amazon just to the Brazilian side of the border look just like parts of the Amazon just to the opposite side of the border. This obviously isn't bullet-proof - you might worry that governance, institutions, infrastructure, populations, languages, etc change discontinuously at the border. They do some initial checks to show that this isn't true (including a nice anecdote where the Brazilian president-elect accidentally walked into Boliva for an hour before being stopped by the border patrol), which are decently compelling (though we're always worried about unobservables). Under this assumption, BCO run an RD comparing deforestation rates in Brazil to its neighbors:

The first key figure from BCO: in 2000, well before Brazil's aggressive anti-deforestation policies, the percent of forest cover was much lower on the Brazilian (right-hand) side of the border.

There's a clear visual difference between deforestation in Brazil and in its neighbors. But here's what I really like about the paper: even if you don't completely buy the static RD identifying assumption here, you have to agree that the following sequence of RD figures is pretty compelling.

This is a little annoying to compare to the first figure, since the y-axis here is different: this time, it's percent of forest cover lost each year - that's why Brazil appears higher in these figures than in the earlier graph. But: it clearly pops out that In 2006, when Brazil's policies went into effect, the discontinuity disappears.

The cool thing about the data that the authors have, which differentiates it from many spatial RD papers, is that it's not static - they've got multiple years of data. This allows them to look at deforestation over time. Critically, even though Brazil's forest cover is much lower than its neighbors prior to the policy, its annual rate of forest cover loss slows dramatically in 2006, when the deforestation policies came into effect, and appears to remain equal to the neighboring country rate in 2007 and 2008. 

This is pretty strong evidence that the anti-deforestation policies put into place by the Brazilian government worked! You should still be slightly skeptical, and want to see a bunch of robustness checks (many of which are in the paper), but I really like this paper. It combines awesome remote sensing data with a quasi-experimental research design to study the effectiveness of important policies. It's not too often that we can be optimistic about the future of the Amazon - but it looks like we've got some reason to be hopeful here.

If you've made it all the way through this post, I'll reward you with John Oliver's new video on science.

Out of the Darkness and Into the Light? Development Effects of Rural Electrification In India

At long last, Louis and I have a working paper version of our paper, "Out of the Darkness and Into the Light? Development Effects of Rural Electrification in India" (Appendix here - warning: it's a pretty big file). The paper has, as you might expect, a lot of gory details in it, and the appendix even more so, so I'll try to provide a less technical overview here. 

The basic motivation behind the paper is the following: there are still over a billion people around the world without access to electricity, most of whom are poor, rural, and live in South Asia or Sub-Saharan Africa. Developing country governments and NGOs are pouring billions of dollars into rural electrification programs with the explicit goal of bringing people out of poverty - one of the new UN Sustainable Development Goals is to "Ensure Access to Affordable, Reliable, Sustainable and Modern Energy for All."

In light of the big pushes towards universal energy access (pun only half intended), it's important that we understand what these investment dollars are going towards - even more so when we're talking about developing country dollars, which have opportunity costs like schools and health clinics and roads. It turns out, though, that we know surprisingly little about the actual effects of electrification on economic development. There is a strong positive correlation between GDP per capita and electricity consumption, with rich countries like the USA and Japan consuming much more energy per capita than poorer places like Nigeria and Bangladesh:

Data source: World Bank

As we all know, though, correlation does not equal causation (thanks, XKCD!). Figuring out the causality here is definitely not trivial: at the country level, there are lots of things that drive income differences between Japan and Bangladesh that have nothing to do with electricity. It turns out that these omitted variable bias problems plague sub-national-level studies as well. If we just regressed incomes (or better yet, welfare!) on electricity infrastructure at the village level in a developing country (say, India), we'd likely end up with a number that was way too high. Why? Energy infrastructure projects are large and expensive, and (correctly) not randomly placed: governments think long and hard about where to put the electricity grid. In practice, this usually means that places that are already doing well economically, or places that are expected to do well in the future, are the first to get access to electricity. In more technical terms, that regression I described above is subject to a ton of omitted variable bias. 

In our new paper, Louis and I try to shed light on the following question: What does electrification do to rural economies? To do this, we take advantage of a natural experiment built into India's national rural electrification program, RGGVY, which would eventually expand electricity access in over 400,000 villages across 27 states. In order to keep costs down, in the first phase of the program, only villages with neighborhoods of 300+ people were eligible for electrification. This means that we can compare villages with 299-person neighborhoods to those with 301-person neighborhoods to look at the effect of electrification. The idea is that, in the absence of RGGVY, these villages would be virtually indistinguishable - and indeed, in the paper, we show that prior to the program, villages just above and just below the 300-person cutoff look the same. Having a cutoff of this kind built into the program is really nice from an evaluation standpoint, because it allows us to mimic a randomized experiment couched in the natural (large-scale) rollout of RGGVY. 

Having identified this cutoff, we get to bring a bunch of cool data to bear on the problem. The first thing we need to do is to demonstrate that RGGVY actually led to increases in electricity access for eligible villages. We're concerned that a simple 1/0 electrification indicator doesn't actually capture power availability and use - it would mask variation in power quality or in the number of households that have access to the grid, for example. Instead, we turn to remote sensing. We got access to boundary shapefiles (outlines) of [almost] every village in India, and superimposed them on top of NOAA's DMSP-OLS nighttime lights dataset - this is a satellite-based measure of nighttime brightness. We combine these to datasets and "cookie-cutter" out the nighttime lights values for each village, which allows us to create statistics like the average or maximum brightness in each location.

Yum, village cookies!

We pair nighttime brightness data from 2011, 6 years after the announcement of the program, with population information from the 2001 Census (the official population of record for RGGVY), and look at the effects of eligibility for RGGVY on night lights. Another advantage of the cutoff-based ("regression discontinuity", for those in the know) analysis? It lends itself naturally to blogging, because you should be able to see the difference between ineligible villages and eligible villages very clearly in a figure. Et voila:

Effects of eligibility for RGGVY on nighttime brightness. Each dot contains ~1,800 villages.

We find that RGGVY eligibility (aka crossing the 300-person threshold) led to a sharp increase in nighttime brightness, as visible from space - remember that we're looking at villages of around 300 people, so we're pretty impressed that we can detect this. It helps that we're studying India, where there are upwards of 30,000 villages in our main estimation sample. It's a little hard to interpret this effect directly, since it's in units of brightness points, but previous papers that have gone out and groundtruthed the relationship between nighttime lights and electrification suggest that this is consistent with about a 50-percent increase in the household electrification rate in our sample. We do a bunch of work in the paper and in the appendix to show that these changes are actually attributable to RGGVY - if you're curious, check it out!

Okay, great: it looks like RGGVY brought electricity to Indian villages - but what about the effects of electricity access on things we care about, like the workforce, asset ownership, housing stock characteristics, village-wide outcomes, and education? We gathered a bunch of village-level data from the Indian Census of 2011 and the District Information System for Education, and look, among other things, at the effects of electrification on outcomes like men and women working in agriculture vs. the more formal sector; ownership of assets like TVs and motorcycles; whether households are classified as "dilapidated" or have mud floors, and other housing stock outcomes; the presence of mobile phone coverage, agricultural credit societies, and other village-wide services; and the number of children enrolled in primary and upper-primary school. Here's a snapshot of (some of) our results:

For all of the outcomes I've shown here, we see very little evidence of sharp discontinuities at the 300-person threshold. We do see clear evidence of men shifting from agricultural to non-agricultural employment (see p. 20 in the paper), but little else. The graphical evidence is borne out by the regression estimates as well: in almost no cases can we reject the null hypothesis of zero effect, but more importantly, we can reject even modest effects in nearly all outcomes. (The exception to this is education: we again see no visual evidence of effects on education, but our sample size is much smaller for these outcomes, since not all villages actually contain schools, so we have less precision with which to rule out effects; the schools effects are also sensitive to specification choices, bandwidths, etc in a way that the other outcomes are not.) To reiterate: in the medium term, we find that eligibility for RGGVY caused a substantial increase in electricity use, but can reject small effects on labor markets, asset ownership, housing characteristics, and village-wide outcomes; we do not find robust evidence that RGGVY led to changes in education. We were pretty surprised by these results, so we threw a bunch of checks at them (see the Appendix) - but they seem to hold up. (Turns out that our results are also consistent with new evidence from our Berkeley colleagues Ken Lee, Ted Miguel, and Catherine Wolfram in Kenya - see the abstract here).

A couple of these tests in particular are worth highlighting:

You might be concerned that we're not finding much because the program wasn't implemented well, or because we're lumping a bunch of villages where electrification did a lot in with villages where electrification didn't do anything, so things are averaging out to zero. When we cherry-pick the states that saw the largest increase in nighttime brightness as a result of the program, however, we don't see evidence of this. Among this selected sample, the nighttime lights effect approximately doubles - but the effects on the other outcomes stay the same. 

You might also be concerned that villages with around 300 people are unlikely to see big effects - they might be too poor, too credit-constrained, etc, etc, etc. A couple of responses to this: first, if we care about electrification from a poverty-reduction standpoint, then we should be worried about people being too poor to take advantage of electrification. But that's more speculative than data-driven, so we do a more formal test to think about effects of electrification for the rest of the villages in India. Rather than relying on our nice cutoff, we instead do a difference-in-differences (DD) analysis: we compare villages electrified in the first wave of the program (like a "treatment" group), before and after electrification, to villages electrified in the second wave of the program (like a "control" group). When we do this, and calculate different effects by population groups, here's what we find:

There are a couple important takeaways from this figure: first, our cutoff-based estimate (navy dots) line up remarkably well with the DD point estimates for the appropriately sized villages; and second, the brightness effect is increasing in population, but the other outcomes (proportion of men working in agriculture shown here) are not, suggesting that our original estimates might actually generalize to the rest of the population. 

So what does it all mean? We present well-identified quasi-experimental evidence from the world's largest unelectrified population. Taken together, our results suggest that rural electrification may not be as beneficial as previously thought. Does our paper say that we shouldn't be implementing these kinds of electrification programs, or that electricity isn't making people better off? No - we explicitly don't make any statements about overall welfare in the paper, because we don't have the data to support these types of claims. In fact, we visited some villages in Karnataka in December, which made it pretty clear that people like having access to power (so do I!). But we can say that it's difficult to find evidence in the data that electrification is dramatically transforming rural India after 5 years or so. We think this is a case where highlighting a null result is really important - take that, file drawer! At the end of the day, in the medium term, rural electrification just doesn't appear to be a silver bullet for development. In typical Ivory Tower fashion, we think more research is needed to understand where and when power can transform economies - maybe we should be targeting electricity infrastructure upgrades to urban areas, for instance. We've got a couple projects in the works to look at some of these questions - so check back with us in a few years, and hopefully we'll have some more answers!