evaluation

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. 

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!

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. 

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 MatsaHanson 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!


Weekend Op-Ed: Delhi driving restrictions actually work [so far]!

New semester, new blog-resolutions. We're back with a WWP...except that the analysis I'm talking about here hasn't actually made its way into a working paper yet. That said, the work is interesting and cool, and extremely policy-relevant, so it's worth taking a minute to discuss, I think.

For those of you not up on your India news, Delhi's air pollution is horrendous. Air pollution data suggest that Delhi's PM2.5 and PM10 concentrations are the worst in the world - the city has even less breathable air than notoriously dirty Beijing. Having spent some time in Delhi last January, I can add some of my own anecdata (my new favorite Fowlie-ism) as well: after three days of staying and moving around in the city, I was hacking up a lung trying to walk up three flights of stairs to our airbnb. I'm certainly not the fittest environmental economist around, but a few steps don't usually give me trouble. 

So I was glad to hear that Delhi has recently been undertaking some efforts to improve its air quality. I was less glad to hear the method for doing so: between January 1 and January 15, Delhi implemented a pilot driving restriction. Cars with license plates ending in odd numbers would be allowed to drive on odd-numbered dates only, while cars with license plates ending in even numbers would be allowed to drive on even-numbered dates only. This sounds good - cutting the number of cars on the road by about half should have a drastic effect on air quality, right? The problem is that Mexico City has had a similar rule in place for years -  Hoy No Circula - and rockstar professor Lucas Davis took a look at its effects in a 2008 paper, published in the Journal of Political Economy. Unfortunately (I thought) for the Indian regulation, Lucas finds that license-plate-based restrictions lead to no detectable effect on air quality across a range of pollutants.

Here's Lucas' graphical evidence for Nitrogen Dioxide. If the policy had worked, we would've expected a discontinuous jump downwards at the gray vertical line. He shows similar figures for CO, NOx, Ozone, and SO2.&nbsp;

Here's Lucas' graphical evidence for Nitrogen Dioxide. If the policy had worked, we would've expected a discontinuous jump downwards at the gray vertical line. He shows similar figures for CO, NOx, Ozone, and SO2. 

Lucas provides an interesting possible explanation for the lack of change: he has suggestive evidence that drivers responded to the regulation by buying additional vehicles - in the Delhi case, if I have a license plate ending in 1, but really value driving on even-numbered days, I might go out and get a car with a plate ending in 2 instead. In light of this evidence, I was less-than-optimistic about the Delhi case. 

So what actually happened in Delhi? New evidence from Michael Greenstone, Santosh Harish, Anant Sudarshan, and Rohini Pande suggests that the Delhi driving restriction pilot did have a meaningful effect on pollution levels - on the order of 10-13 percent! (A more detailed overview of what they did is available here). These authors use a difference-in-differences design, in which they compare Delhi to similar cities before and after the policy went into effect, doing something like this:

Effect = (Delhi - Others)_Post - (Delhi - Others)_Pre

Under the identifying assumption that Delhi and the chosen comparison cities were on parallel emissions trajectories before the program went into effect, this estimation strategy is nice because it removes common shocks in air pollution. The money figure from this analysis shows the dip in pollution in Delhi starkly:

It looks like, in its brief pilot, that Delhi was successful at reducing pollution using this policy. So why is the result so different than in Mexico City? Obviously, India and Mexico are very different contexts. It also seems like the channel Lucas highlighted, about vehicle owners purchasing more cars, is something that people would only do after being convinced that the policy would be permanent - so there might be additional adjustment that occurs that isn't picked up in a pilot like this. (Would you go out and buy a new car in response to someone telling you that over the next two weeks they're trying out a driving restriction? I don't think I have that kind of disposable income...) Also, the control group obviously matters a lot. I'd like to see (and expect to see, if this gets turned into an actual working paper) a further analysis of what's going on in the comparison cities over the same time period. The pollutants being measured are different - though I doubt that this actually affects much, given how highly correlated PM is with the pollutants measured in Lucas' paper. 

In general, I'm encouraged to see both that Delhi is taking active steps to attempt to reduce air pollution, and that these steps are being evaluated in credible ways. As the authors point out in their Op-Ed, and as I've tried to highlight above, we should be cautious about extrapolating the successes of this pilot to the long run - a congestion or emissions pricing scheme might be a more effective long-run approach to tackling air pollution.

I'd also like to briefly highlight the importance of making air pollution data available for these kinds of analysis. There's a cool new initiative online called OpenAQ that's trying to download administrative data from pollution  monitors and make this information publicly available - and they're not the only ones. Berkeley Earth is also providing some amazing data on Chinese air quality - and rumor has it they'll be adding more locations soon.  Understanding the implications of air quality on health, productivity, and welfare is increasingly important as developing country cities grow and house millions in dirty environments - the more data that's out there to aid in this effort, the better.

Forget weatherization - how do we make evaluation work?

The New York Times put out an important article yesterday discussing the importance of credible policy evaluation, featuring work by the all-star team of Fowlie, Greenstone, and Wolfram. The upshot of the article? When program evaluation is done by people with a stake in seeing that same program succeed, we have reason to worry about the conclusions. The problem is the following: if non-independent evaluation teams suggest that a program is great, it's hard to know whether it's actually great or if existing incentives distorted the results.  

The Weatherization Assistance Program is a large effort by the US government to weatherize low-income households and make them more energy efficient. The aforementioned all-star team of economists put out a paper in June (now R&R at the QJE!) using a state-of-the-art randomized controlled trial to measure the energy savings from the program. They concluded, much to the chagrin of many energy efficiency advocates, that the costs of the program are twice the energy savings benefits among Michigan households.

Cheery weatherization clipart from  here .&nbsp;

Cheery weatherization clipart from here

The DOE recently released their own study of the program, in over 4,000 pages spread across 36 documents. If you're cynical like me, you're perhaps not shocked that the DOE's report finds that overall, the program benefit-cost ratio is 4:1. This takes into account non-energy benefits such as health that Meredith, Michael, and Catherine did not directly include in their original study (though to be fair, they did look at indoor temperature set-points, and find no evidence of changes - suggesting that there is little propensity for large health effects to result from reduced exposure to extreme temperatures among their sample).

What even a cynical reader might be surprised by is the magnitude of the problems with DOE's reports. From the Energy Institute blog (I also highly recommend that you read the accompanying deep dive into thermal-stress-related benefits):

We have spent many hours poring over these opaque documents. Our judgment is that many of the DOE’s conclusions are based on dubious assumptions, invalid extrapolations, the invention of a new formula to measure benefits that does not produce meaningful results, and no effort to evaluate statistical significance. Using the DOE’s findings, we show below that costs exceed energy savings by a significant margin. We also document major problems with the valuation of non-energy benefits, which comprise the vast majority of estimated program benefits.

Overall, the poor quality of the DOE’s analysis fails to provide a credible basis for the conclusion that the benefits of energy efficiency investments conducted under WAP substantially outweigh the costs. This blog summarizes our assessment of the DOE’s analysis for a general audience. We provide a more technical discussion, using the important example of benefits relating to thermal stress, here.
— Energy Institute at Haas blog, October 6, 2015

Eduardo Porter, author of the excellent New York Times article described above, also conducted a Q&A with Bruce Tonn, head of the DOE evaluation team. If you ask me, this is almost more damning than the original article - but I'll leave you to judge for yourself.

Full disclosure: I provided research assistance on the economists' response, helping to read over the thousands of pages of documents from DOE. So maybe I'm a less-than-impartial commentator. But I will say this: I would have been thrilled to see a DOE report that, using modern empirical techniques and direct measurements, was able to provide definitive proof of the existence of large and real health benefits from WAP. I'm disappointed that the evidence that DOE did provide was appears unconvincing and flawed. Getting climate policy right, and furthermore, getting low-income assistance right, in situations where governments have limited budgets, demands honest, sometimes hard-to-stomach, independent evaluation. Getting these policies right now will pay off in the long run - as will moving towards an institutional culture of proper ex post evaluation.

PPS: Not-at-all-humble brag moment - guess who the "graduate student" mentioned in the NYT article is? Hopefully not my last NYTimes mention...but my own work has a long way to go before being ready for anything like that, so I should stop writing this blog and get to writing a job market paper.

Disclaimer: I wrote this blog post without the supervision or knowledge of Meredith, Michael, and Catherine. I certainly do not speak for them, nor for the E2e project, EPIC, Energy Institute, etc, etc, etc.