WPS5639
Policy Research Working Paper 5639
Beyond Baseline and Follow-up
The Case for More T in Experiments
David McKenzie
The World Bank
Development Research Group
Finance and Private Sector Development Team
April 2011
Policy Research Working Paper 0
Abstract
The vast majority of randomized experiments in such outcomes at relatively short intervals allows the
economics rely on a single baseline and single follow-up researcher to average out noise, increasing power. When
survey. If multiple follow-ups are conducted, the reason the outcomes have low autocorrelation, it can make sense
is typically to examine the trajectory of impact effects, so to do no baseline at all. Moreover, the author shows how
that in effect only one follow-up round is being used to for such outcomes, more power can be achieved with
estimate each treatment effect of interest. While such a multiple follow-ups than allocating the same total sample
design is suitable for study of highly autocorrelated and size over a single follow-up and baseline. The analysis
relatively precisely measured outcomes in the health and highlights the large gains in power from ANCOVA rather
education domains, this paper makes the case that it is than difference-in-differences when autocorrelations
unlikely to be optimal for measuring noisy and relatively are low and a baseline is taken. The paper discusses the
less autocorrelated outcomes such as business profits, issues involved in multiple measurements, and makes
household incomes and expenditures, and episodic recommendations for the design of experiments and
health outcomes. Taking multiple measurements of related non-experimental impact evaluations.
This paper is a product of the Finance and Private Sector Development Team, Development Research Group. It is part of
a larger effort by the World Bank to provide open access to its research and make a contribution to development policy
discussions around the world. Policy Research Working Papers are also posted on the Web at http://econ.worldbank.org.
The author may be contacted at dmckenzie@worldbank.org.
The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development
issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the
names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those
of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and
its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent.
Produced by the Research Support Team
Beyond Baseline and Follow-up:
The Case for More T in Experiments*
David McKenzie, World Bank
Keywords: Randomized Experiments; Multiple Measurements; Program Evaluation.
JEL codes: O12, C93.
*
I thank Chris Woodruff and participants at the Warwick University summer workshop on Firms in Development
for conversations and questions which lead to this article; Chris Blattman, Miriam Bruhn, Jishnu Das, John Gibson
and Berk Özler for helpful comments; Matthew Groh for research assistance; and Miriam Bruhn, Jishnu Das, and
Markus Goldstein for sharing their data.
1. Introduction
The number of randomized experiments being conducted in economics has exploded over the
past decade, especially in development economics. The vast majority of these studies use only a
single baseline and single follow-up survey, or a single follow-up with no baseline. This has
been the case in the early randomized experiments looking at education (e.g. Glewwe et al, 2004)
and health outcomes (e.g. Miguel and Kremer, 2004), and has remained true as experiments have
expanded to consider other interventions and outcomes, such as recent high-profile experiments
in microfinance (Karlan and Zinman, 2010; Banerjee et al, 2010). In the rare cases where
multiple post-treatment survey waves have been conducted, they have been typically taken
relatively far apart in time, with the goal of examining whether the treatment effect differs in the
short-term and medium-term. For example, Banerjee et al. (2007) examine impacts of
educational interventions at one year and two year horizons. Indeed, so much is the paradigm of
baseline plus follow-up accepted that the excellent toolkit for randomization of Duflo et al.
(2008) does not discuss at all the possibility of doing more than one pre-treatment or post-
treatment round of surveying, let alone the choice of how many such rounds.
In contrast, the clinical trials literature has noted the potential advantages of taking repeated
measures of outcomes of interest not just to study the time course of treatment effects, but to
obtain more precise estimates of effects around particular endpoints (Frison and Pocock, 1992).
Vickers (2003) argues that the number of repeat measures should be a key design choice in
conducting experiments, and concludes that the benefit of such additional measures is of greatest
value when the autocorrelation of measures is low, such as with episodic conditions like
headaches. Such a description would certainly seem to fit key economic outcomes like business
profits, and incomes and consumption of the poor. As the recent work by Collins et al. (2009)
makes abundantly clear, one of the key difficulties of living on $2 a day is that people don’t
receive $2 every day, but rather a highly irregular stream of income. Measuring microenterprise
income, in particular, can be difficult, with the resulting data typically having large heterogeneity
in reported profits among reasonably similarly sized firms (de Mel et al, 2009). While some of
this likely reflects measurement error, Fafchamps et al. (2010a) report that Ghanaian
microenterprise owners confirm 85 percent or more of changes in profits above 150 percent or
2
below -60 percent as genuine, reflecting seasonality and the high degree of idiosyncratic
variability facing microenterprise owners.
As a result of the high variability and low autocorrelation in economic outcomes like firm
profits, income, and expenditure among poor households, there is much to be potentially gained
by taking multiple measures of these outcomes at relatively short intervals and averaging over
them when estimating treatment effects. This is the approach used in de Mel et al. (2008), who
use a baseline and 8 quarterly follow-up waves of business profits and in Fafchamps et al. (2010)
which uses two survey rounds before randomization and a further 4 quarterly follow-up surveys.1
However, this approach seems to be the exception rather than the rule. The premise of this paper
is that many field experiments are making a suboptimal choice of how many rounds of surveys to
collect, and that the default choice of a single baseline and single follow-up study is unlikely to
be optimal in many cases. This paper aims to combine insights from the medical literature on
repeated measurement, new analysis of the formulae underlying power calculations, and
experience from these studies using multiple measures in economics to provide a practical guide
for researchers designing experiments. While our discussion will be in terms of experiments,
many of the same issues and therefore lessons also apply for design of non-experimental impact
evaluation designs, such as matched difference-in-difference estimation.2
An additional contribution of the paper is to draw to the attention of empirical researchers in
economics the large improvement in power that can arise when estimating treatment effects via
an Analysis of Covariance (ANCOVA) estimation compared to using the more common
difference-in-difference specification. The improvement in power is greatest when the
autocorrelation is low – intuitively when the baseline data have little predictive power for future
1
Bloom et al. (2010) provides an example of very large T, with 114 weekly observations on firm output, quality,
and inventory levels.
2
Gibson and McKenzie (2010) provide an example where multiple rounds of follow-up data are averaged to get
more precise measurements of consumption and income in a matched difference-in-differences impact evaluation of
a seasonal migration program. One key difference with non-experimental evaluations is that the presence of a
baseline becomes more valuable to allow one to control for baseline differences across individuals; whereas
randomization ensures these baseline differences are balanced on average. In addition, multiple rounds of pre-
treatment data are also of additional use in non-experimental studies to show parallel trends in difference-in-
differences analysis, or to rule out or control for the presence of pre-program effects like an Ashenfelter dip.
Multiple pre- and post-treatment data can also be combined to conduct overidentification tests to distinguish
between different data generating processes (Ashenfelter and Card, 1985).
3
outcomes, it is inefficient to fully correct for baseline imbalances between treatment and control
groups.
Section 2 begins with a theoretical discussion of what power calculations tell us about the
gain to be had from using more rounds of data, and provides examples for common types of
economic data. Section 3 then derives implications for the choice of how many pre-treatment and
post-treatment waves to use. The bottom line is that collecting multiple measurements post-
treatment will make most sense when the data have low autocorrelation; whereas baseline data is
of most use when the autocorrelation is high (although there are of course other important uses of
baseline data apart from improving the power to estimate treatment effects, such as for
examining treatment heterogeneity, and so one may still wish to do a baseline for these other
reasons – something I discuss at the end of the paper). It would appear that for many economic
outcomes, experiments with a fixed budget to conduct a total of K surveys would have greater
power when dividing that K over multiple post-treatment rounds than having a baseline and
single follow-up. Section 4 then discusses additional practical issues which are likely to arise
when considering multiple measurements in economic experiments, many of which are not
common concerns in clinical trials. Section 5 concludes.
2. What is the gain from more rounds?
Let Yi,t be an outcome of interest for household or firm i in survey round t.
Consider an intervention which assigns units to receive a binary treatment (such as getting
business training or not, or getting a conditional cash transfer or not). Suppose there are m pre-
treatment survey rounds (labeled –(m-1) through 0) and r post-treatment survey rounds (labeled
1 through r). A common method in economics for estimating the treatment effect 3 of the
intervention on the outcome of interest is via the following difference-in-differences
specification:
(1)
where EVERTREATi is a dummy variable which takes value one if unit i is assigned to the
treatment group and zero if it is assigned to the control group, the are time dummies, and
3
I focus on estimation of intention-to-treat effects here, but the same points made here also apply for measurement
of the treatment effect on the treated and other treatment effects of interest.
4
TREATi,t takes value one if unit i has been assigned to receive treatment by time t (that is for
t=1,2,…r), and zero otherwise. The treatment effect of interest is then given by γ.
Note that γ does not contain a t subscript: either the treatment is assumed to have a
constant level effect, or the treatment effect of interest is taken to be the average treatment effect
over the r post-treatment rounds. Clearly a further, very important, use of multiple post-
intervention surveys is to collect information on the trajectory of treatment impacts (e.g.
Woolcock, 2009), since the short and long-run impacts of some policies may differ dramatically.
However, unless one imposes some structure on the form these impact trajectories can take,
collecting more rounds of data merely increases the number of points in time at which these
impacts can be measured, but does not improve the power of an experiment for measuring these
impacts. Even in this case where impacts at different points in time are of interest, one can
consider multiple measurements located around each time horizon of interest, and thereby
improve power. For example, if a study is interested in knowing whether the impact of
microfinance differs at a one year horizon versus a three year horizon, taking measures of
microenterprise profits at 11, 12 and 13 months after treatment, and at 35, 36, and 37 months
after treatment can be used to improve the accuracy of impacts at around these horizon points, by
assuming the treatment effect is constant or considering an average treatment effect in the
neighborhood of the horizon of interest. The analytics and ideas of the remainder of the paper
can then be applied to estimating the impact at a particular horizon by taking more measurements
in neighborhoods around these horizons.
2.1.The case of a single baseline and single follow-up
Consider first the case of a single baseline and single follow-up. Then we see that the
least squares estimator of γ is simply the difference in means between the treatment and control
groups at follow-up less the difference in means between the treatment and control groups at
baseline:
(2)
Then sample size to detect a given treatment effect at a specified power level and significance
level is a linear function of the variance of this estimator. Assume the are independent across
individual units with cross-sectional variance σ2, but may be autocorrelated over time for the
5
same unit, with autocorrelation ρ. The variance of the difference-in-differences estimator is then
easily seen to be 4σ2(1- ρ)/n where n is the size of the treatment and control groups. Compare
this to the simple “post” estimator, which uses only the difference in means for the follow-up
survey, ignoring the baseline:
(3)
which has variance 2σ2/n. From this we observe the following:
Implication 1: With a single baseline and follow-up, difference-in-differences only gives more
power than the post estimator which ignores the baseline data when the autocorrelation is greater
than 0.5.
A more efficient method of estimation than difference-in-differences is to control for the baseline
levels of the outcome of interest and estimate the following4:
(4)
Let be the least squares estimator of θ, then the estimator of the treatment effect coming from
equation (4) is called the ANCOVA estimator
(5)
Frison and Pocock (1992) show that ANCOVA is more efficient than either difference-in-
differences or analysis using only the post data, with a variance approximately proportional to
2σ2(1- ρ2)/n.5 We therefore deduce:
Implication 2: When the data have zero autocorrelation, there is no gain from using baseline
data. Otherwise the ANCOVA estimation in equation (4) offers more power than either the
commonly used difference-in-differences estimation or estimation based on follow-up.
Intuitively, when the autocorrelation is low, the baseline data are not very informative for what
future values of the outcome of interest will be. Controlling fully for observed baseline
4
Such a specification is estimated in Banerjee et al. (2007) among others.
5
This is an approximation as the need to estimate θ causes a loss of one degree of freedom and also adds a term to
the variance to reflect the sampling error. Both of these terms are negligible in any reasonably-sized randomized
experiment, and hence are ignored here.
6
differences in the mean outcome via difference-in-differences is therefore over-correcting for
differences which don’t have much predictive power, whereas the ANCOVA estimation adjusts
the degree of correction for baseline differences in means according to the degree of correlation
between past and future outcomes actually observed in the data.
The ratio of the difference-in-differences variance to the ANCOVA variance is 2/(1+ ρ). So
when ρ=0, with a single baseline and follow-up, one would need twice the sample size when
using difference-in-differences to get the same power as obtained with ANCOVA. When ρ=0.25,
which we will see to be a reasonable estimate for several economic outcomes, the sample size
needed is still 60% higher with difference-in-differences than with ANCOVA to get the same
power. There are therefore important gains in power to be had from not using difference-in-
differences to estimate treatment effects with standard economic variables.
This comparison of the ANCOVA and difference-in-difference estimators in terms of efficiency
is appropriate for experimental estimation, where both estimate the same average treatment
effect. However, in non-experimental estimation, the estimators also require different
assumptions for efficiency. Imbens and Wooldridge (2009, p. 70) discuss this issue.
2.2. Multiple rounds pre- or post-treatment
Now consider the general case of m pre-treatment survey rounds and r post-treatment survey
rounds. The difference-in-differences estimator is obtained by estimation of equation (1). This
can be written as:
(6)
Where for
is the mean of the outcome for treatment or control group g in the post-treatment period, and n is
the number of cross-sectional observations assigned to treatment and to control. The pre-
treatment means are defined analogously.
7
Frison and Pocock (1992) give a general formula for the variance of , which depends on the
full pattern of autocorrelations across the different time periods. For power calculations, one
needs to make simplifying assumptions as to how these autocorrelations behave. Frison and
Pocock assume equal variances for all time points, equal correlations between all pairs of time
points, and that autocorrelations are equal for the treatment and control groups. They show for
physical health measures like cholesterol, blood pressure, and CD4 cell count that this
assumption of constant autocorrelation is reasonable. In the next subsection I show such an
assumption may also hold approximately for key economic outcomes. Then assuming the
treatment and control groups are each of cross-sectional size n, the variance of the difference-in-
differences estimator is shown by Frison and Pocock to be:
Under these same assumptions, the variance without any baseline surveys of the difference in
post-treatment means is then:
Equations (7) and (8) are respectively the variances used in power calculations under the
“POST” and “CHANGE” methods reported in STATA’s sampsi command. We therefore see
that:
Implication 3: With m baselines and r follow-ups, difference-in-differences only gives more
power than the post estimator which ignores the baseline data when the autocorrelation is greater
than 1/(m+1).
Not surprisingly, fact 3 shows that the more baseline rounds of data there are, the more likely it
is that it is costly to ignore them. However, as with the single baseline case, if the data are only
weakly autocorrelated, it can be costly in terms of power to fully control for baseline differences
in means via difference-in-differences.
8
As with the single baseline and follow-up case, ANCOVA estimation will be more efficient than
both difference-in-differences and estimation using only the follow-up data. The ANCOVA
estimator with multiple pre- and post-treatment rounds is:
This can be estimated via the following least squares regression for t=1,2,..,r for individual i:
(10)
where It is very rare
for economists to collect more than one round of data pre-treatment, so such an equation has not
been typically estimated in practice for more than one pre-treatment round.
Under the same assumptions as used to derive (7) and (8), the variance of the ANCOVA
estimation is then approximately:
This is the formula used in power calculations under the ANCOVA option using STATA’s
sampsi command.
Implication 4: If the autocorrelation is zero, then only the number of post-treatment survey
waves affects the power of the ANCOVA estimator, there is no gain from baseline surveys, and
it reduces to the POST estimator. Intuitively, an autocorrelation of zero means that each round
the outcome is a mean plus noise. The treatment changes the mean, and more post-treatment
rounds enables one to better average out this noise.
2.3. Autocorrelations in practice for economic experiments
As noted above, the formulae given for the variances of the different estimators assume that the
autocorrelations are equal between all points in time, and that they are equal for the treatment
and control groups. For power calculations to be useful, we need not have these assumptions
9
hold exactly, but we need them to be a reasonable approximation. The next sub-section then
discusses what to do in cases when this assumption doesn’t hold.
The assumption that the autocorrelations are equal between all points in time is one that many
economists may have second thoughts about for both theoretical and statistical reasons. On the
theoretical side, if we think that a large source of the period-to-period variation in economic
outcomes like profits, income or consumption comes from temporary shocks, we should expect
the impact of these shocks to die out over time, so that observations closer apart in time will be
more highly correlated than those further apart in time. Statistically, constant (non-zero)
autocorrelations imply that although the data generating process is covariance-stationary, it is
non-ergodic for the mean and thus a law of large numbers will not apply to the mean of as the
time dimension approaches infinity.
However, while such an assumption may therefore not be appropriate globally over all horizons,
it may be a reasonable assumption within the likely time horizons of many applications. That is,
while we might not believe the correlation between business profits this month and next month is
the same as that between this month and 10 years from now, the correlation between this month
and next month may be close to that between this month and two months from now. For
example, in a local neighborhood of a particular time horizon, a reasonable data generating
process for might be , where is i.i.d. noise. Thus, for example, within a
few months around the one year after an intervention horizon we might expect profits for a
particular firm to be higher or lower depending on some longer-term shock , and then in
addition from month to month the firm gets idiosyncratic demand shocks which cause its profits
to move around further.
Ultimately it is therefore an empirical question as to whether this assumption seems reasonable
over the periods of typical economic experiments, and especially over short-term neighborhoods
of a few months around a particular horizon of interest. Figures 1A, 1B, and 1C investigate this
assumption for microenterprise profits and for household expenditure. Figure 1A shows
autocorrelations for monthly profits from the Sri Lankan microenterprises in de Mel et al. (2008)
which were measured at three month intervals, and uses data from similar microenterprises
measured monthly in de Mel et al. (2009) to show the autocorrelation in monthly profits at the
one month and two month horizons. A horizontal line is drawn at 0.38, which is the average
10
autocorrelation over the different interval measures. Pointwise confidence intervals for these
autocorrelations are obtained via 1000 bootstrap replications. While Figure 1A does suggest
some tendency for the autocorrelation to fall as the time horizon increases, the data do not
deviate much from the 0.38 level over all time horizons between 1 month and 18 months, and so
the assumption of constant autocorrelation seems a reasonable approximation here.
Figure 1B shows the autocorrelations in monthly microenterprise profits in urban Ghana, which
were measured at three month intervals in the experiment of Fafchamps et al. (2010b), and
Figure 1C shows the autocorrelation in three monthly household expenditures from the same
experiment, also measured at quarterly intervals. Horizontal lines are drawn at 0.32, the mean
autocorrelation over these horizons for profits, and 0.20, the mean autocorrelation over these
horizons for household expenditures. Again both figures suggest the assumption of constant
autocorrelation holds approximately over these horizons.6 Gibson et al. (2003) also provide
evidence from Zambia and urban China that the autocorrelation of expenditure does not change
very much within a year as one increases the number of months between surveys.
Table 1 then considers the evidence for the second part of the assumption, which is that the
autocorrelations are the same for treatment and control, using the microenterprise profits data
from Sri Lanka and Ghana. The point estimates in most periods are reasonably similar between
treatment and control, and the bootstrapped confidence intervals for the difference in
autocorrelation between the two always contain zero. Evidence from another setting comes from
using the test score data of Banerjee et al. (2007). The verbal test score autocorrelation is 0.58 for
the treatment group and 0.61 for the control group; and the math test score autocorrelation is 0.47
for the treatment group and 0.55 for the control group. Therefore in these samples this
assumption seems reasonable.
Table 2 provides autocorrelations from other data sets for a range of different economic
outcomes. The purpose of this is twofold. First, it demonstrates that for many economic
outcomes, the autocorrelations are typically lower than 0.5, with many around 0.3. An exception
is test scores, which have higher autocorrelations. Second, it provides some parameters that
researchers can use when conducting their own power calculations, since it is rare to have
6
The Sri Lankan microenterprise surveys only measured household expenditure annually, which is why household
expenditure is not shown for this sample.
11
autocorrelation data available for the study populations being considered. We see from Table 2
that autocorrelations are often in the 0.2-0.3 range for household income and consumption. In
rural Ghana, the autocorrelation in Boozer et al (2010)’s data is 0.32 when wives report on both
their own and their husband’s consumption, but increase to 0.58 to 0.66 when husbands and
wives report separately on consumption and the results are combined. The autocorrelations are
lower for the poor – in both Mexico and Argentina the autocorrelation of labor income is around
0.2-0.3 for individuals with first period labor income below the median, compared to
autocorrelations of 0.5-0.8 for those with this income above the median. This is consistent with
the evidence in Collins et al. (2009) that incomes for the poor are very volatile.
The autocorrelation will typically be lower in the more homogeneous samples typical of many
randomized experiments than it is in general samples of the population. It will also be lower if
one stratifies the randomization or uses fixed effects and thereby controls for time-invariant
reasons why one household or firm may have higher income, expenditure or profit levels than
another. To see this in a simple example, write the error term , where X is a
characteristic that is used to stratify the randomization on, or to restrict an experiment only to
individuals with certain values of X. Then:
And
Controlling for X via stratified randomization, or restricting the sample only to those with certain
values of X will therefore reduce the variance of , which increases the power of an
experiment. However, it also reduces the autocorrelation (by removing a factor which would
otherwise cause the error term to be correlated from one period to the next), thereby increasing
the value of more measurements.
2.4. What should one do if the autocorrelations are not constant?
The empirical evidence therefore suggests that the assumption that the autocorrelation is constant
over different time horizons and is the same for the treatment and control is likely to be a
12
reasonable approximation in a number of economic experiments. How do violations from this
assumption affect power calculations?
For post and difference-in-difference analysis, one can simply use the mean autocorrelation in
the power calculations. Since the variances of these estimators are linear in , power calculations
using the mean will still give the correct power for these estimators even when the
autocorrelation differs between treatment and control groups or over different time periods. In
contrast, since the variance of the ANCOVA estimate is decreasing in , using the average
will understate the sample size one would actually need to achieve a given power. In such cases
using the minimum expected among follow-up rounds would be conservative.
3. Implications for choosing the number of pre-treatment and post-treatment rounds
Equations (7), (8) and (11) can be used to help researchers decide how many rounds of data they
should collect before and after the treatment. We use these formulae to examine implications for
choice of the number of pre-treatment and post-treatment rounds.
3.1. Given a fixed T of 3 or more rounds, how should they be split between pre-treatment
and post-treatment?
The first question we ask is how a researcher who has decided on fielding multiple survey rounds
should split these rounds before and after treatment. To do this, we solve for the choice of r and
m which minimizes the variance given r+m=T.
Implication 5: The optimal choice of r = T/2 = m for difference-in-differences estimation, and
this choice does not depend on the autocorrelation in the data. When is odd, the power is
the same when choosing m-r=1 as r-m=1, that is, when allocating the extra odd wave to pre-
treatment or to post-treatment.
Proof: Setting r+m=T in equation (7) and solving for the optimal choice of r to minimize the
variance gives the first part of this result. Re-writing the variance in (7) as
13
Shows that r and m contribute symmetrically to the variance of the difference-in-differences
estimator, and so that choosing r = (T+1)/2 and m=(T-1)/2 will yield the same results as
choosing r=(T-1)/2 and m=(T+1)/2
Intuitively, in a difference-in-differences design, differences in pre-treatment means have exactly
as much weight in the estimator as differences in post-treatment means, and so the optimal
strategy is to have the same number of time periods to estimate the difference pre-treatment as
post-treatment. Note from (12) that while the autocorrelation does not affect the choice of how to
allocate the survey rounds between pre-treatment and post-treatment in a difference-in-
differences design, it does affect the cross-sectional sample size needed – a higher
autocorrelation reduces the variance, thereby requiring a smaller n.
Implication 6: For ANCOVA estimation, the optimal choice of r given fixed T is given by
So when ρ=0.5, the optimal choice is r = (T+1)/2, whereas when ρ=0.25, the optimal choice of r
= (T+3)/2.
Proof: Expanding out the variance in (11), one sees that r and m are symmetric in the numerator.
Minimizing the variance therefore amounts to maximizing the denominator, r[1+(m-1) ρ], which
can be solved to give the expression in (13).
Thus with ANCOVA estimation, one chooses fewer pre-treatment survey rounds the lower is the
autocorrelation. Intuitively, we see in equation (9) that the pre-treatment difference in means
contributes less to the estimator than the post-treatment difference in means, and so it is less
important to accurately measure the pre-treatment difference than to accurately measure the post-
treatment difference. When the autocorrelation is low, this can result in choosing to have no
baseline. For example, when T=3 and ρ=0.25, the optimal choice is r=3, so one is better to have
3 follow-up waves and no baseline than a baseline and two follow-up waves.
14
3.2. Given a fixed total sample size nT, what is the trade-off between a larger cross-section
and more survey rounds?
In many cases a researcher will face a fixed total budget, which can fund K=nT total surveys.
They must then decide between carrying out a larger cross-sectional sample, which gives
information on more units, and carrying out more survey rounds, which gives more information
on each unit. Taking K as fixed, we derive the optimal division into more rounds versus more
individuals per round.
Implication 7: For POST estimation, the optimal choice is T=1 and n=K when ρ>0, and all
values of T and n such that nT=K yield the same power when ρ=0. When ρ<0, the power is
higher using T=2 and n=K/2 than it is using T=1 and n=K, while the assumption of constant
autocorrelation across different points in time doesn’t make sense for negative autocorrelation
and T>2.
Proof: From equation (8) we can see that when rn=K, the variance depends on (r-1) ρ, so the
optimal choice of r to minimize this will depend on ρ in the way stated.
This fact is analogous to the decision in a clustered randomized trial of whether to collect more
observations per cluster, or more clusters. With clustered randomization, since randomization is
at the level of the cluster, if there is positive intra-cluster correlation, there is more power to be
had in randomizing over more clusters than in having fewer clusters and a larger sample per
cluster. Likewise here the randomization occurs in the cross-section, and so with positive
autocorrelation, there is more gain to having more cross-sectional units than more observations
in the time dimension on each unit.
Implication 8: For difference-in-differences estimation, the choice of how to allocate a fixed
sample K between n and T does not affect the variance provided that one then chooses to allocate
T equally between pre-treatment and post-treatment rounds (as in Fact 5), and that there is at
least one baseline and one follow-up to enable difference-in-differences estimation.
Proof: Setting r=m=T/2 and nT=K in (12) yields a variance of which does not
depend on either T or n.
15
Thus the power of difference-in-differences estimation is the same with a single baseline and
follow-up and n=100, as it is with two pre-treatment rounds and two post-treatment rounds and
n=50. Intuitively, with difference-in-differences, every observation counts equally in calculating
the pre-treatment and post-treatment means which form the basis of estimation.
This result of course depends on the assumption of equal correlation being a reasonable one. So
this implication is likely to make sense when choosing between one or two follow-up surveys, or
even between one and five follow-up surveys, but should not be taken to the extreme of saying
we should expect the same power from T=100 and n=2 as we would from T=2 and n=100.
Implication 9: With ANCOVA estimation, when the autocorrelation is high it is better to do a
larger cross-section and fewer survey rounds, whereas when the autocorrelation is low, it is
better to do relatively more survey rounds and a smaller cross-section. Holding nT fixed, with a
single baseline: (i) the optimal value of r holding nT fixed is ; (ii) two follow-up
surveys will offer more power than a single follow-up survey for ρ<0.5; (iii) three follow-up
surveys will offer more power than one or two follow-up surveys for ρ<1/6.
Proof: Set m=1 and nT=K in (11), and then take the derivative with respect to r to show (i).
Compare the variances with r=1, 2, and 3, to show (ii) and (iii).
Therefore when the total sample size is fixed at K, power will typically be greater using a
baseline and 2 post-treatment surveys with a cross-sectional sample of K/3 than a single baseline
and follow-up for many types of economic data. But it will be rare in practice for more than two
post-treatment surveys to be optimal with a fixed total sample size. However, the standard
practice of a single baseline and single follow-up used in so many economics experiments is
unlikely to be the optimal choice for all.
In practice the cost of adding another cross-sectional unit versus surveying the same unit a
second time can differ. In many experiments there can be large fixed costs of adding additional
units to the experiment. These fixed costs can include the costs of screening and enrolling more
subjects in the study, the cost of the intervention itself (many times this is by far the largest cost),
and potentially the cost of more handheld units for surveying them. Denote the fixed costs of
another cross-sectional unit by a. There can also be fixed costs of conducting another survey
round, such as the need to pay field managers for more months of work. Denote the fixed cost of
16
another time round by b. Finally denote the marginal cost of another survey, whether cross-
sectional or temporal, by c. Then, assuming only one baseline, with a fixed budget D, one can
solve for the optimal number of follow-up rounds and cross-sectional units by minimizing the
ANCOVA variance in (11) subject to an+br+cn(r+1) = D.7 This does not have a closed form
solution, but can easily be solved numerically for specific cases. For example, take ρ=0.30, b =
$100 and c = $50, and D = $500,000. Then with a relatively cheap treatment of a = $100, the
optimal is to take n=1200 and r=2 follow-ups, whereas with an expensive treatment of a =
$10,000, the optimal is to take n=27 and r=21 follow-ups. Thus studies with more expensive
treatments should optimally collect more data on each unit treated.
3.3. What is the marginal gain to another post-treatment round?
Finally, in many experiments researchers have a fixed cross-sectional sample, often dictated by
the pool of eligible applicants for some pilot program they are investigating. For example, an
NGO has money to offer a treatment to 1000 farmers, or a government wishes to pilot a program
in 50 villages. The question then facing the researcher is how many survey waves to collect.
Consider the difference-in-differences estimator, and the gain in power from collecting r+1
rounds compared to r rounds of post-treatment data. This gain in power is proportional to the
difference in the variances, and so using (12) we have:
Difference-in-difference Gain = (14)
Note that the gain in power from adding more post-treatment rounds to difference-in-differences
is the same as the gain to adding more post-treatment rounds to estimation by the post method,
and thus the gain in (14) is the same as that calculated by Vickers (2003) for the case of
estimation by the post method. Using (11), we see that this is also the gain in power from adding
more post-treatment rounds to ANCOVA estimation.
7
This assumes that the treatment and control groups are the same size. When the cost of adding another treatment
greatly exceeds that of adding another control, optimal power with a given budget can be achieved by allocating
more units to the control group than to the treatment group (See Duflo et al, 2008). Conditional on doing this, it may
still be optimal to allocate fewer cross-sectional units to more survey rounds.
17
Implication 10: There are diminishing marginal returns to adding more post-treatment rounds in
terms of the gain in power they give. The greatest gain is from moving from one to two post-
treatment rounds, and the gains are smaller the higher is the autocorrelation.
Proof: One can easily determine that the derivatives of (14) with respect to both r and ρ are both
negative.
Given the symmetry of the role of pre-treatment and post-treatment surveys in difference-in-
difference estimation, we see the same holds for adding more pre-treatment rounds. For
ANCOVA estimation, the gain from adding pre-treatment rounds is different from that from
adding post-treatment rounds in general, and the gain from moving from one to two pre-
treatment rounds is less than that from moving from one to two post-treatment rounds when
3.4. Numerical illustrations
To illustrate how much the required cross-sectional sample size can be reduced when more
survey rounds are undertaken, Table 3 presents the minimum treatment group size n obtained
under power calculations with different values of r, m, and ρ. I consider a hypothetical
experiment intended to detect a 10 percent increase in business profits from a baseline value of
100. Microenterprise profits are noisy, so it is common for the standard deviation to be of the
same order of magnitude as the mean. I therefore take the standard deviation as 100, and fix the
power at 80 percent and size at 5%. Panel A then shows the treatment group sample sizes
required for post estimation, Panel B for difference-in-differences estimation, and Panel C for
ANCOVA estimation, for ρ ϵ{0, 0.25, 0.5, 0.7, 0.95}. It is assumed that the control group is the
same size as the treatment group in these calculations.
Table 3 illustrates numerically Implications 1-6, and Implication 10. Comparing the sample sizes
in Panel A and B, we see Implication 1 and 3. When there is only one baseline, difference-in-
differences requires larger sample sizes than post analysis when ρ<0.5, the same sample sizes for
ρ=0.5, and lower sample sizes for ρ>0.5. The difference in sample size can be large. For
example, with a single baseline and follow-up, when ρ=0.25, one would need a treatment group
size of 2355 with difference-in-differences, compared to 1570 with post analysis. Adding a
second pre-treatment survey reduces the sample size for difference-in-differences to 1766,
18
consistent with Implication 3 (with 2 baselines, difference-in-differences only has more power
than post for ρ>1/3). Comparing Panels A and B to Panel C we see consistent with Implications
2 and 4 that ANCOVA requires the same sample size as post when ρ=0, and otherwise requires
lower sample sizes than either difference-in-differences or post. Thus in the case of a single
baseline and follow-up and ρ=0.25, ANCOVA requires a treatment group size of 1472,
compared to the 1570 with POST and 2355 with difference-in-differences. We see in particular
that ANCOVA does substantially better than difference-in-differences when ρ is low, and
substantially better than POST when ρ is high.
Panel B also illustrates Implication 5. For a fixed number of waves T, the required sample size is
smallest when the numbers of pre-treatment and post-treatment waves are equal. Thus with T=4,
the treatment sample size required with ρ=0.5 is 785 with 2 pre-treatment waves and 2 follow-
ups, compared to 982 with one baseline and three follow-ups. We also see the sample sizes
required when m=1 and r=2 are the same as those with m=2 and r=1. In contrast, as per
Implication 6, we see ANCOVA favors more post-treatment waves than pre-treatment waves
when ρ is low. Thus the treatment sample size required with ρ=0.5 is 785 with one baseline and 2
follow-ups, compared to 1047 with two baselines and 1 follow-up.
Finally in Table 3 one can also observe Implication 10, the diminishing gain from adding more
survey rounds, with the amount of the gain lower the higher is ρ. Thus for difference-in-
differences with one baseline, when ρ=0 the gain from going from one to two post-treatment
waves is a reduction in the treatment group size of 785, whereas the gain in going from two to
three post-treatment waves is only 261. When ρ=0.95, the gains are only a reduction in
treatment size of 39 when going from one to two post-treatment waves, and 13 in going from two
to three post-treatment waves.
Table 4 illustrates the differences in power obtained in changing the allocation of a fixed total
sample size between n and T. We fix nT = 1000, and consider different combinations of cross-
sectional and time series samples. Again we assume a mean and standard deviation of 100, and a
treatment effect of 10 percent. Panel A illustrates Implication 7, showing that T=1 is always best
when ρ>0 for POST analysis. Panel B illustrates Implication 8, demonstrating that the power is
the same regardless of how n and T are split, so long as r=m=T/2. Finally, Panel C illustrates
Implication 9, that for a given total sample, sometimes power can be greater when doing a
19
baseline and multiple follow-ups, than by doing a single baseline and single follow-up. For
example, when ρ=0.25, power is greater doing one baseline and two follow-ups with n=333,
than doing a single baseline and single follow-up with n=500, but also greater than doing one
baseline and three follow-ups with n=250.
As a final illustration, consider the power to detect an impact of microfinance on business
profits. Banerjee et al. (2010) report a mean of 550 and standard deviation of 46604 for business
profits. With such noisy data, the treatment and control group sample sizes required to detect a
10% increase in profits with 90 percent power using a single baseline and follow-up are over 15
million! Suppose then that they were able to consider a more homogeneous set of firms and
measure profits more accurately8, reducing the standard deviation to 550. Then assuming an
autocorrelation of profits of 0.25, with their sample of approximately 1150 treatment and 1150
control, the power for detecting a 10% increase in profits would be 0.669 with a single cross-
section post-treatment, 0.697 with a baseline and single follow-up, 0.892 for a baseline and two
follow-ups, and 0.952 with a baseline and three follow-ups.9 Likewise, taking the example of
Karlan and Zinman (2010), who have a control group mean of 17,000, if the standard deviation
were the same as the mean, the power to detect a 10% increase in profits would rise from 0.68
with a single post-treatment survey as they have to 0.902 for a baseline and two follow-ups and
0.958 with a baseline and three follow-ups. In both cases then, assuming the standard deviation
of profits can be kept or reduced to a reasonable level, the choice of a second or third post-
treatment measure would allow them to detect a treatment effect of interest with considerably
more power than possible with only a single survey round.
4. Recommendations for practice and other practical issues
The above analysis has shown that there are gains to be had from moving beyond the paradigm
of single baseline and follow-up. In this section I discuss first some basic guidelines for using
these results in practice, and then discuss other practical issues that might affect the choice of
how many survey waves to carry out.
8
They construct profits as revenue less expenses. De Mel et al. (2009) show that this leads to considerably noisier
profit measures than directly asking for a single profits number in their experiments.
9
These power calculations ignore intra-cluster correlation for simplicity, and because it is typically low for an
outcome like profits.
20
4.1. Guidelines for practice
1. Highly autocorrelated outcomes: For outcome measures like anthropometric measures or test
scores, for which the autocorrelation is high (e.g. ρ=0.6 to 0.8), always include at least one
baseline. Difference-in-differences and ANCOVA have much greater power than POST in these
cases. Moreover, Bruhn and McKenzie (2009) also show that the power improvements from
stratified or matched randomization are highest when ρ is high. However, if the total sample size
is fixed, a single baseline and follow-up will offer more power than multiple pre-treatment or
post-treatment rounds when ANCOVA is used. If the treatment and control sizes are fixed, the
gains from going from one to two post-treatment surveys can still be non-trivial in these cases,
but there is little gain from more than say 3 post-treatment surveys.
2. Outcomes with low autocorrelation: For outcome measures like business profits, incomes, or
expenditure, for which the autocorrelation is typically low (e.g. ρ=0.20 to 0.40) , it can be
optimal to have no baseline at all, and just do a single follow-up survey if the total sample size is
limited. If the treatment group size is fixed, researchers can dramatically increase power by
doing multiple post-treatment surveys. Even if a baseline is taken, researchers should not use
difference-in-differences in such cases, since doing so has much lower power than either POST
or ANCOVA analysis.
4.2. Other practical issues
In practice there are several other factors that should guide researchers in choosing how many
survey rounds to conduct. I note some of the key factors here, and their implications for choice
of the number of pre-treatment and post-treatment waves:
1. Over what horizon is a pooled treatment effect relevant and of interest? The analysis in
this paper has assumed a common treatment effect γ. Of course if the treatment effects
vary over individuals, researchers are usually content to estimate an average treatment
effect, and the analysis here will still hold. However, in some experiments the effect of
the treatment may also vary over time. In this case estimation of γ by pooling multiple
post-treatment survey waves will yield an average treatment, where the average is over
multiple waves. If the survey waves are relatively close together in time (e.g. monthly or
quarterly), then combining several post-treatment waves and getting the average
21
treatment effect over a period 9-15 months post-treatment is likely to be reasonable.10 In
contrast, if there is reason to believe the effects differ dramatically with time since
treatment, one will not want to average over long periods. High seasonality may provide
another reason to conduct multiple measures – it may be of more interest to get the
average impact over high and low demand periods than to get the impact only at one
particular point in time.
2. Survey compliance and attrition. Conducting multiple survey waves increases the burden
on respondents, which might increase attrition. Using multiple pre-treatment waves can
be beneficial in this respect, by eliminating the individuals most likely to attrit before the
randomization is done, one can improve internal validity by randomizing only over
individuals that are likely to be found in a follow-up survey. In contrast, if multiple
rounds of post-treatment surveys cause significant attrition, this will limit the extent to
which researchers will wish to conduct many rounds of the survey. If the survey is just
collecting measurement of a few key outcomes, these additional rounds of post-treatment
surveys can be short and less burdensome for respondents, which can minimize this drop-
out. Secondly, by conducting multiple post-treatment rounds, researchers stand a better
chance of capturing at least once post-treatment individuals who are harder to track
down. For example, a business owner who travels temporarily to other towns might get
missed in a one-off survey, but may get found when going back at monthly or quarterly
intervals. Finally, there is also the possibility that waiting for a long time to re-contact
people may make it harder to find them, and make respondents think you have lost
interest in them, whereas regular follow-ups may instead these risks.
3. Will multiple measures change people’s reporting or people’s behaviors? Experience
with measuring microenterprise profits suggests that respondents may report more
accurately after one or two rounds of surveys, perhaps as they better understand the
concepts being asked and can recall them better when asked for a second or third time
(Samphantharak and Townsend, 2009; Fafchamps et al, 2010a). This suggests a benefit to
researchers of conducting more than one pre-treatment survey. However, in some
circumstances there will be a concern that asking the same question multiple times will
10
Researchers interested in time since treatment effects can then combine multiple measures around 1 year, around 2
years, etc. See De Mel et al. (2008) for an example, in which quarterly waves are combined to look at how treatment
effects vary over the first year since treatment, second year since treatment, etc.
22
either change the way people respond, or their behavior. For example, Zwane et al.
(2010) summarize the results of five experiments in which the frequency of surveying
was varied. They find being surveyed more frequently lowers reported child diarrhea
rates and leads to more use water treatment products and take-up of medical insurance.
However, they find no effect of being surveyed on borrowing behavior. The risk is
therefore that in some settings and for some outcomes, repeated surveying may serve as
reminders to increase the salience of neglected actions. Finally, repeatedly asking
individuals the same questions may change reporting due to fatigue. For example,
individuals who are repeatedly asked about expenditure may quickly learn that they can
reduce the length of the questionnaire by saying “no” to questions which when answered
positively lead to lengthy detailed questions about what was spent.
4. Cost considerations. Surveying a smaller cross-section over multiple survey waves can
result in a different cost than doing a larger cross-section single baseline and follow-up.
Whether the cost is higher or lower will depend on country context. On one hand, a
smaller cross-sectional sample with more survey waves allows a smaller survey team to
be used for longer periods of time, potentially resulting in higher average quality
enumerators. In addition, it can lower the costs of listing since a smaller cross-sectional
sample is used. Of greatest cost savings in many experiments is that it also avoids the
costs of paying for the intervention for as many units. On the other hand, the team is in
the field for a longer period of time, which can raise costs. As a general rule, the higher
the per-unit treatment cost, the more likely it is that doing multiple measures per unit
treated is optimal.
5. Learning by doing. Even in cases where researchers have some power to detect a
treatment effect with one post-treatment survey round, it can be useful to plan multiple
survey rounds relatively close together in time. This allows researchers to quickly
analyze the early results from the first follow-up survey, and based on these, ask follow-
up questions in the next post-treatment survey to explore new hypotheses generated by
the results.
6. How do we know what ρ is? Power calculations already require substantial insights from
researchers in terms of what the likely mean, standard deviation, and treatment effect size
of interest are. Pilot surveys or existing data are often used to give some sense of likely
23
parameters. In most cases researchers will not have data on the autocorrelation of the
outcome of interest. It is hoped that the data provided in this paper for different outcomes
from different surveys will therefore provide a starting point for researchers, and that
more researchers will report these autocorrelations in future experiments.
7. Can we just obtain multiple measures more cheaply by recall? A cheaper alternative to
conducting multiple post-treatment or pre-treatment rounds is to ask multiple
measurements in a single survey, with recall. While intuitively appealing, the value of
this approach is likely to be limited in practice, since it is precisely the types of variables
that are noisiest and hardest to measure in practice for which the data are typically less
autocorrelated and for which multiple measures are of most value. For small informal
firm owners who do not keep books, asking profits with recall over multiple months is
difficult, while asking expenditure month by month or quarter by quarter with recall is
likely to be highly inaccurate. Gibson and Kim (2010) show even with wage workers in
the United States that retrospective recall is problematic, with workers underreporting
transitory variation in earnings, creating non-classical measurement errors. However,
such a strategy could be used in cases where good records are available, such as in
experiments with larger firms which have accurate books or records.11
8. To baseline or not? The power calculations above suggest that, in a number of cases, it
can be optimal in terms of power to conduct a single post-treatment survey of size n=K
than to do a baseline and follow-up with n=K/2. However, there are several other factors
to consider in choosing whether or not to use a baseline. A baseline can be used to stratify
the randomization on key variables, improving power and providing a basis for
examination of treatment effect heterogeneity. It is often used to examine what
determines take-up of some intervention. It can be useful for verification of
randomization in cases where there is a risk of the randomization not being implemented
perfectly, and can also be used to test whether attrition is non-random in terms of baseline
characteristics. Finally a baseline, and especially multiple pre-treatment surveys, offer the
possibility of matched difference-in-differences as a back-up evaluation strategy in cases
11
See e.g. Bloom et al. (2010) who collect daily and weekly production data from plants with over 100 workers each
once a month.
24
where there is a risk that the randomization may not get implemented in practice or a risk
that take-up of a program may be lower than anticipated.
However, when the outcome has low autocorrelation, the baseline does not reveal very
much about likely future outcomes, and thus can be an expensive undertaking.
Researchers attempting to implement large-scale evaluations with governments or NGOs,
where there is reasonable uncertainty as to whether randomization will actually be carried
out and whether they will have sufficient take-up. For example, consider a micro-savings
intervention, where a government or NGO agree to randomly choose villages in which to
introduce a new savings product. There is a risk that after doing baseline surveys in the
treatment and control villages that the government changes its mind, and decides to
introduce the product in all villages (or decides not to introduce the product at all). There
is also a risk that no one uses the new product, in which case there is no possibility of
measuring the impact of savings accounts on household outcomes. In such a case,
practical considerations may suggest it is optimal to not carry out a baseline, and then
wait and only carry out post-treatment surveys if the product is indeed randomly
introduced and take-up is high.
5. Conclusions
This paper has shown that when the autocorrelation in outcome data is low, as is common with
outcomes of interest like business profits, expenditure, and income, the standard paradigm of
single baseline and follow-up, followed by difference-in-differences analysis, is unlikely to be
optimal. Large improvements in power can be obtained from multiple post-treatment measures in
experiments with fixed treatment and control group sizes, and from using ANCOVA instead of
difference-in-differences. Researchers choosing how to allocate a fixed budget over multiple
surveys may find they can obtain more power by not conducting a baseline at all, and if they use
a baseline, will often get more power doing two follow-up waves with a smaller cross-sectional
sample size than a single follow-up with a larger cross-sectional sample.
These findings are particularly likely to be of interest and use to researchers conducting
experiments with interventions to help the poor, since the profits, incomes, and expenditures of
25
the poor are typically more volatile and less autocorrelated than those of stable wage earners for
example. In many cases the size of the treatment group is determined by the number of units
eligible for some pilot initiative, and so hopefully researchers can extract much more out of these
samples by considering multiple measurements.
26
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29
Figure 1: Is the Autocorrelation approximately constant over different time horizons?
1A: Sri Lanka Microenterprise Profits
0.80
0.70
Autocorrelation in Monthly Profits
0.60
0.50
0.40 Autocorrelation
Confidence
0.30 Interval
0.20
0.10
0.00
0 3 6 9 12 15 18
Months between Measurements
1B: Ghanaian Microenterprise Profits
0.80
0.70
Autocorrelation in Monthly Profits
0.60
0.50
0.40 Autocorrelation
Confidence
0.30
Interval
0.20
0.10
0.00
0 3 6 9 12 15
Months between Measurements
30
1C: Ghanaian Household Expenditure
0.5
Autocorrelation in Three Monthly Expenditure
0.4
0.3
Autocorrelation
0.2 Confidence
Interval
0.1
0
0 3 6 9 12 15
Months between Measurements
Table 1: Does the autocorrelation change with treatment status?
Ghana Sri Lanka
Microenterprise Microenterprise
Profits Profits 95% C.I. for Profits Profits 95% C.I. for
Control Treatment difference Control Treatment difference
Correlation between Baseline and:
t=2 0.148 0.334 (-0.11, +0.46) 0.413 0.464 (-0.14, +0.25)
t=3 0.451 0.440 (-0.43,+0.33) 0.375 0.390 (-0.18, +0.13)
t=4 0.382 0.462 (-0.37,+0.44) 0.387 0.357 (-0.18, +0.11)
t=5 0.323 0.504 (-0.21,+0.47) 0.393 0.242 (-0.35, +0.07)
t=6 0.313 0.578 (-0.28, +0.64) 0.282 0.324 (-0.15, +0.20)
Average N: 325 344 220 318
Notes:
Time periods correspond to calendar quarters.
31
Table 2: Examples of Autocorrelations for Other Economic Outcomes
Outcome Source Country Time Interval ρ
Household Income Gibson and McKenzie (2010) Tonga 6 months 0.38-0.47
Vanuatu 6 months 0.19-0.21
Household Expenditure Gibson and McKenzie (2010) Tonga 6 months 0.12-0.33
Vanuatu 6 months 0.35-0.53
Boozer et al. (2010) Ghana 6 months 0.32 (single-report)
0.58-0.66 (separate reports)
Gibson et al. (2003) Urban China 2, 4 and 6 months 0.15-0.18
Individual Labor Income EPH May and October 2002 Argentina 6 months Below median income: 0.25
(see McKenzie, 2004) Above median income: 0.79
ENE 2003:1-2004:1 Mexico 3 months Below median income: 0.29-0.31
(see Bruhn, 2011) Above median income: 0.50-0.53
6 months Below median income: 0.22-0.31
Above median income: 0.49
Math test scores Das et al. (2007) Zambia 1 year 0.68
Andrabi et al. (2010) Pakistan 1 year 0.61
Banerjee et al. (2007) India 2 years 0.59
Language test scores Das et al. (2007) Zambia 1 year 0.68
Andrabi et al. (2010) Pakistan 1 year 0.65-0.66
Banerjee et al. (2007) India 2 years 0.51
32
Table 3: How does the cross-sectional sample size required vary with
correlation and rounds
Panel A: Sample Sizes required with Post Estimation
Pre Post p=0 p=0.25 p=0.5 p=0.7 p=0.95
0 1 1570 1570 1570 1570 1570
0 3 524 785 1047 1256 1518
0 5 314 628 942 1194 1507
1 1 1570 1570 1570 1570 1570
1 2 785 982 1178 1335 1531
1 3 524 785 1047 1256 1518
1 4 393 687 982 1217 1511
2 1 1570 1570 1570 1570 1570
2 2 785 982 1178 1335 1531
2 3 524 785 1047 1256 1518
3 2 785 982 1178 1335 1531
4 1 1570 1570 1570 1570 1570
Panel B: Sample Sizes required with Difference-in-Differences
Pre Post p=0 p=0.25 p=0.5 p=0.7 p=0.95
1 1 3140 2355 1570 942 157
1 2 2355 1766 1178 707 118
1 3 2094 1570 1047 628 105
1 4 1963 1472 982 589 99
2 1 2355 1766 1178 707 118
2 2 1570 1178 785 471 79
2 3 1309 982 655 393 66
3 2 1309 982 655 393 66
4 1 1963 1472 982 589 99
Panel C: Sample Sizes required with ANCOVA
Pre Post p=0 p=0.25 p=0.5 p=0.7 p=0.95
1 1 1570 1472 1178 801 154
1 2 785 883 785 566 114
1 3 524 687 655 487 101
1 4 393 589 589 448 95
2 1 1570 1413 1047 665 117
2 2 785 825 655 430 78
2 3 524 628 524 351 65
3 2 785 785 589 373 65
4 1 1570 1346 942 578 98
Notes: Power calculations calculated for hypothetical experiment
with Control mean and standard deviation of 100,
treatment effect size of 10%, size 0.05 and power 0.80.
ANCOVA with p=0 is the same as POST estimation. 33
Table 4: How does power vary with n and T holding nT fixed?
Cross-sectional Number of Number of
Sample Pre-treatment post-treatment
n rounds (m) rounds (r) p=0 p=0.25 p=0.50 p=0.75 p=0.90
Panel A: Post
1000 0 1 0.609 0.609 0.609 0.609 0.609
500 0 2 0.609 0.516 0.447 0.394 0.368
250 0 4 0.609 0.394 0.293 0.237 0.213
Panel B: Difference-in-Differences
500 1 1 0.201 0.252 0.353 0.609 0.942
250 2 2 0.201 0.252 0.353 0.609 0.942
250 1 3 0.162 0.201 0.278 0.491 0.865
100 5 5 0.201 0.252 0.353 0.609 0.942
Panel C: Ancova
500 1 1 0.353 0.372 0.447 0.667 0.952
333 1 2 0.446 0.405 0.446 0.636 0.932
250 2 2 0.353 0.339 0.410 0.641 0.948
250 1 3 0.491 0.394 0.410 0.575 0.889
100 5 5 0.353 0.299 0.379 0.622 0.945
100 1 9 0.564 0.274 0.249 0.332 0.604
Note: Power calculations calculated for hypothetical experiment with control mean and standard
deviation of 100, treatment effect size 10%, and size 0.05.
34