Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
The Experimental Political Scientist
In this issue
• Eckel and Wilson on Collabo-
ration
• McDermott and Dawes on
Biopolitics
• Leeper on Protocol
• Gailmard on Morton/Williams
book
• Dunning on Blocking
• Fredickson on Balancing
• Announcements
From the Editor
Welcome to the next issue of the Experimental
Political Scientist. We
have two new, hopefully recurring
features: notes on across field collaboration
and a book review of
a recent book directly engaging
with experimental political science.
We also have two feature sections,
one on bio-politics and one on the
role of blocking and randomization
tests. Finally, we have a follow-up
on experimental protocol. Happy
experimentation! Dustin Tingley,
Harvard Government Department
Information on Joining or
Contributing
The Experimental Political Scientist
is the official newsletter of APSA
Organized Experiments section 42.
To receive the newsletters register
for the section ($8/yr!)
at http://www.apsanet.org
and visit us at http://psexperiments.ucr.edu/group.
Graduate
students and professors are
highly encouraged to submit to the
newsletter. This and the previous
issues provide examples for submission
themes. Questions can be
sent to the editor. Deadline for the
fall newsletter will be 10/15/2011.
Letter from the President: A Golden Era for the Gold
Standard?
The experimental method is often referred to as the gold standard
for causal inference. The founding of this section reflects disciplinary
recognition that the experimental method has become a
common part of political scientists’ toolkit. Other signs of the penchant
towards experimentation can be found in the dramatic rise,
over the past decade, of published articles using the experimental
method, and the publication of several books on experiments in political science.
This should not, however, be taken as indicative that a golden era of experimental
political science has arrived. Designing, implementing, and analyzing a good
experiment brings with it a host of challenges that often escape notice, even to
experimenters themselves. It is exactly now - as experimental approaches continue
to spread through the discipline - that high standards must be upheld and educational
efforts be undertaken. I am confident that this section and its contributors
will take a leading role in such initiatives. Along these lines, the section has taken
a number of steps to facilitate experimental research, keep members connected
with the latest developments in experimental political science, and offer particular
opportunities for young scholars. Here is a sampling of our activities:
A junior scholars committee that plans to institute a mentor match program at
APSA so that graduate students and recent Ph.D.s can meet with more senior scholars
to discuss their research; an experimental standards committee that is working
to develop standards for reporting social science experimental research (the committee’s
suggestions will be distributed and discussed among section members);
and a journal committee that is assessing the pros and cons for starting a new experimental
political science journal. These efforts are reinforced by our newsletter
and section website.
Of course the section also undertakes what all other sections do: organize
APSA panels. This coming APSA will be the first in which the section has panels,
thanks to the able organizational efforts of section head Kevin Arceneaux. Kevin
received many more proposals than he could accommodate given the limited number
of spaces allocated by the APSA. The best way for the section to receive more
panels in 2012 is to come to the 2011 panels - APSA allocates slots based, in part,
on attendance of the prior year’s section’s panels.
The section will not host a reception at APSA; instead, our plan is to use funds,
as they grow, to set up small research grants for junior scholars’ experimental research.
Most such funds come from section membership fees, and thus, if you
have not already joined, I implore you to do so. It only costs $8! I also encourage
everyone to attend the section’s business meeting at APSA where we will discuss
work by the aforementioned committees and present book, paper, and dissertation
awards.
This is an exciting time for experimental political science but one that requires
our action and involvement. For the experimental method to play an increasing
role in producing knowledge about government and politics, it is critical that steps
be taken to ensure high standards.
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
The Odd Couple? Co-authoring across
disciplinary boundaries.
Catherine C. Eckel
Economics, UT-Dallas
eckelc@utdallas.edu
Rick K. Wilson
Political Science, Rice
rkw@rice.edu
The Editor of this Newsletter asked us why we work
together, and how we navigate the cross-disciplinary divide.
We come from different disciplines and we speak
(somewhat) different languages, but in our own work we
use the same methodology. As a result, our skill sets are, to a
large extent, substitutes rather than complements. Yet we
have written a great deal together and have developed a
common interest in questions that cut across numerous
disciplines. Perhaps our experience has some relevance for
understanding co-authorship more generally.
We first met at the Public Choice Society meetings in
1986. The Public Choice meetings once had a significant
representation of experimental research, though that is less
true now. Many economists interested in experiments
attended these sessions. Because of the focus on collective
decision making and voting, there also was a small
contingent of political scientists, sociologists and the
occasional psychologist attending. Both of us were
presenting papers on strategic voting and until that point we
had not realized we were working on a similar topic. Rick
looked a little different in those days: he had very long hair
and maybe even a beard - he’s since abandoned the hippy
professor look. Catherine’s paper, with Charlie Holt, was
published in the AER and cited Rick’s paper. Rick’s paper,
with Bobbi Herzberg, was published in the JOP and Rick
cited Charlie properly, but misspelled Catherine’s name (you
can look it up). After that we proceeded to ignore each other
for 10 years.
We ran into one another at the National Science
Foundation in 1996 where we were both starting as Program
Officers for our respective disciplines. We were fortunate in
that there was a large group of fellow Program Officers in
our division who were also interested in using experiments.
This prompted daily lunches and discussions of our own
work among all of us. Like many co-authorships, this one
started with one of us (Wilson) walking into the other’s
office (Eckel) and tossing a paper on the desk, pronouncing
that the authors had done it all wrong. As usual, Catherine
asked Rick to be specific, rather than general, and we quickly
designed an experiment to test a key feature of the paper.
Little did we realize that this was the start of a long-term
co-authorship.
What Do We Each Bring to the Table?
With most co-authorships the co-authors each bring
unique skills to the table. In this case it is not immediately
obvious that this is the case. Both of us have used
experimental designs for many years. Both of us have a
passing acquaintance with theory and econometrics. As
noted above, we appear to be substitutes rather than
complements. Is this the best mix for scholars?
Despite the similarities, we speak different languages,
we read different things, we approach questions differently,
and we write differently. Catherine is an economist and Rick
is a political scientist. While the language barrier is not
huge, we have realized that in a co-authorship it is important
to have an overlapping vocabulary sufficient to communicate
effectively and precisely. Catherine often complains that Rick
is not being sufficiently precise with a concept (and often she
is correct). This leads to better organized papers and clearer
implications for our findings. Our disagreement over
language usually forces precision.
While we read a good deal of the same work, we are
constantly egging one another on to read new articles. A
typical email exchange might go: “You’ve got to take a look
at this!” “Why? I’m busy.” “You’ll see.” Sure enough, the
article usually fits in with some old problem or serves as
fodder for some new idea that we might want to tackle.
Being able to share in our reading habits (running across
neuroscience, biology, psychology, anthropology, and our
own disciplines) is extremely fruitful. It allows us to quickly
distill ideas and press forward on new topics.
We approach questions differently. Catherine, in the
tradition of Economics, sees a problem, quickly figures out
how it fits with the current disputes. Rick sees the problem
and wants to immediately put it into the larger context.
Catherine pinpoints the precise literature to which the
question is addressed. Rick writes an intellectual history
leading up to the problem, which Catherine then deletes.
These are disciplinary differences and we have learned to
navigate our stylistic differences.
We write differently. Rick’s writing is bloated (this
mostly is Rick’s writing). It wrestles over various ideas and
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
approaches and often takes a while to come to a conclusion.
Catherine’s writing is focused and to the point. Over the
years we have figured out how to best work together - Rick
writes and Catherine cuts. The product is always better for
the joint production.
So far we have detailed the differences. Where we have
a common view is with experimental design. We take design
seriously and often draw on each other even outside our
own co-authorships. Four eyes are better than two when
designing an experiment. We have avoided some major
errors over time by thoroughly working over our designs.
Co-Authorships
One of the major concerns, especially for junior faculty,
is the merit of co-authorships. Rick often hears senior faculty
arguing that junior faculty must demonstrate their
competence by producing single-authored work. Yet this
seems to fly in the face of what is happening in the major
journals. It seems that fewer single authored articles
succeed. Multiple authored articles are becoming the norm
in political science. In experimental economics (and
economics more generally) multiple authorships are
common. It is difficult to imagine how a single author can
elaborate a theoretical contribution, design an experiment
and carefully navigate the minefield of econometrics.
Moreover, to successfully craft a paper that makes a
contribution in more than one discipline is doubly difficult
with a single author.
Here are some simple suggestions. Do not follow our
example. It is useful to seek out co-authorships in which
your skills complement those of others. Experimental design,
as we all know, is exceedingly hard work. Getting the
experiment right is imperative (without internal validity, we
have nothing to say). Make certain that everyone knows the
role you played (and it is probably with the experimental
design). Of course you need to worry about the theoretical
underpinnings of the experiment. And you need to worry
about the empirical component of the paper. But, your
contribution should be clear.
Do not be afraid to step across disciplinary boundaries.
Well, be a little afraid. It is important to be clear about what
you expect to get from such a relationship, especially if you
are untenured. Will your Department value consorting with
an Economist (or, gasp, a Political Scientist)? Will your
Department understand the journal that you publish your
experiment in and how will it count that contribution? In
many economics departments, publications in other fields even
in Science or Nature - just won’t count. Economists are
narrow minded that way. Will your Department count
citations outside the discipline? These are questions that you
should ask. Eventually disciplines will learn to value
cross-disciplinary work. However, there is some burden on
you to make it clear the contribution to your own discipline.
While it can be very rewarding to work with a senior
scholar in your or another field, we advise that you seek out
co-authors who are peers. It is also good not to work all the
time with one coauthor, as that makes your contribution
harder to distinguish come tenure time. Rather than working
with a senior faculty member, develop a cohort of people
who share common interests. In this manner you won’t be
seen as simply the experimental “hired gun” who has no
ideas and makes no contribution outside the lab. (We should
note that the hired gun approach has been very successful
for one or two people we know, so nothing is absolute.) It is
important to signal ownership of an idea, best achieved by
having evidence of a research program, with or without
coauthors. But coauthors, especially those outside your own
discipline, can help develop your research agenda and
highlight its relevance.
Long-term co-authorships can be very rewarding.
Catherine and Rick have worked together for some time. Yet
both of us have other co-authors we have worked with for
even longer periods of time. Long-term co-authorships can
come to resemble old marriages - we often finish one
another’s sentences. An added benefit is that, at conferences
that we jointly attend, we always have a dinner partner to
depend on.
What We’ve Learned From One Another
Rick has gotten a great deal out of this collaboration.
Prior to working together Rick had a rigid view of theory,
hypothesis construction and the role of experiments in
tackling questions. Catherine got Rick to question
anomalous findings and to be willing to go beyond the
narrow confines of political science. Catherine was Rick’s
introduction to Behavioral Economics.
Catherine is surprised to hear this. When we were at
NSF we funded (jointly or in collaboration with other
programs) the first neuro-economics experiments, the first
internet experiments, the first economics experiments with
kids, and lots of stuff that crossed disciplinary boundaries.
We were a bit notorious for championing “risky” research
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with mixed reviews. Together we read Tooby and Cosmides,
Daly and Wilson, Pinker, Matt Ridley, and others, and for the
first time began really to think about connections between
biology and economic/political behavior. This sure was a lot
of fun! And Catherine is pretty sure she wasn’t the leader in
all this!
We develop our ideas together, and we design together.
Rick generally supervises the programming, or does it
himself. Rick is also absolutely great at the first draft! For
Catherine, writing is slow and deliberate, but after a long
conversation, Rick can whip out a first draft in minutes!
In the conferences we attend, and in the summer
courses we teach for PhD students in political science, Rick
likes to cultivate a persona that is grumpy and critical. He
fools a lot of people. But underneath all that he is much
more patient and kind than Catherine. In working - and
especially in teaching - with him, Catherine has learned to
listen more carefully and patiently, and to extract
experimental designs from the fuzziest of student ideas. Still
it is true that Rick spends more time and is more generous
with his groups that she is with hers.
At the moment Catherine wishes that Rick were not
editing the AJPS. He says it “only” takes him four hours a
day. We haven’t written a new paper in, what, three years?
Oh dear, time to get back to work!!
Future of Experimental Approaches to
Biopolitics
Rose McDermott
Brown University
Rose McDermott@brown.edu
Experimental tests of political phenomena have achieved
increasing relevance and credibility over the last decade,
largely lead by developments in American politics related to
the investigation of voting behavior. More recent extensions
of field experiments into this arena both in the United States
and elsewhere have continued to expand this trend.
Meanwhile, extensive experimental tests of the influence of
biology, physiology and genetics on complex social behavior
have taken place outside the field, but few of these
applications have related to politics. Attempts to join these
two traditions, while rare, represent an important
opportunity for those wishing to undertake experimental
investigations into new venues in political science.
The standard dependent variables that tend to be
explored by political scientists, specifically those related to
voting behavior, remain unnecessarily restrictive. Although
such variables constitute the bread and butter of the field,
and certainly represent important and easy variables to
investigate experimentally, other large, complex and
important social and political variables can, and should, be
investigated experimentally as well. The most obvious exist
at the overlap of behavior economics and comparative or
international political economy, including topics quite
amenable to experimental exploration, including foreign
direct investment and foreign aid, perceptions of monetary
and welfare policies, and issues surrounding trade
imbalances and dependencies between allies and
adversaries. Although many of these issues may not appear
to be obviously investigated from the perspective of
biological and genetic issues, they are in fact conjoined at an
underlying conceptual level by theoretical suppositions
regarding the nature of in-group and out-group relations, as
well as larger topics related to the nature of cooperation,
trust and aggression.
Political science as a discipline fundamentally revolves
around the examination and exploration of issues of power,
just as psychology concentrates on those related to affiliation
and economics focuses on those involved in money. As a
discipline, we might be best served by playing to our
strengths, and working to develop experimental tests of
those substantive areas related to our disciplinary strength,
while working in collaboration with those in other fields, to
explore the basis of dominance and power from a biological
and genetic substrate. It would not be surprising, given what
recent studies have shown in the primate literature, to
discover the phylogentic roots of dominance in ancient
instantiated psychological mechanisms. Recent work has
been able to demonstrate these phenomena in macque
monkeys using an adapted version of implicit association
tests. Such work might also illuminate the ways in which
particular local geographies and ecologies may potentiate
individual and regional population variances across
genotypes, as the work of Joan Chaio has shown in her work
on status and dominance across regions. Using genetic
assays and functional magnetic resonance imaging,
increasing number of people in social neuroscience and other
areas have begun to explore these topics in very innovative
ways, using sophisticated experimental paradigms.
Experimental examination of topics related to voting
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and economics, just like those related to dominance, while
crucial for our understanding of important political behavior,
rely in critical ways in theories, methods, and models
derived from other fields. This sort of collaboration, while
not new, needs to transform from the traditional borrowing
model favored by political scientists who tend to use theories
and methods developed in other fields to illuminate
substantive issues of concern in political science, to more
actively contribute our knowledge to broader
interdisciplinary and collaborative teams exploring issues of
substantive interest together. Political science can bring a
strong method to the table by incorporating the use of
surveys and extended interview protocols in the
experimental exploration of the biological basis of complex
social and political behavior. These tools can be used to help
contextualize the relationship between genotype and
phenotype within critical developmental pathways. This
strategy can help illuminate the variety of crucial
environmental triggers which can contingently cue particular
behavioral repertoires, many of which have been extensively
explored in previous work in political science. This
conjoining of past substantive theoretical work and
methodological strategies in political science with novel
explorations of the biological contributions to instigating,
maintaining and curtailing complex social and political
choice opens up an important new avenue for experimental
exploration. Such a research agenda can help enlighten the
complex ways in which biology, environment and culture
reciprocally interact to encourage some behavior while
extinguishing others, and provide insight into how and why
individuals differ in their ability and willingness to direct
and control others to join together to cooperative achieve
goals which range from construction to destruction.
Chris Dawes
University of California at San Diego
cdawes@ucsd.edu
The genopolitics literature took a major step forward
when Alford, Funk, and Hibbing (2005), motivated by
earlier work published by prominent behavior geneticists,
demonstrated that variation in political ideology could be
attributed to genetic variation. Scholars have since found
evidence of heritable variation in a wide variety of political
behaviors and attitudes including voter turnout, strength of
partisan attachment, political efficacy, political knowledge,
interest in politics, and measures of overall political
participation. The work-horse research design employed by
these studies relies on comparing traits of sibling pairs with
differing genetic relatedness to back out estimates of
heritability. Consequently, they do not tell us which genetic
variants are correlated with political behaviors and attitudes
but rather the influence of genes in total.
A subsequent wave of genopolitics research has sought
to identify specific genetic variants that are correlated with
political behaviors. This can be done using one of two
approaches. The first is a theoretical approach that focuses
on ”candidate” genes based on hypotheses about how the
known functions of the genes could be related to the
mechanisms underlying political behavior. Thus far, political
scientists have focused on genes previously shown to be
related to traits such as pro-social attitudes and behavior.
The second approach, known as a genome-wide association
study, interrogates hundreds of thousands or millions of
variants located across the genome looking for a correlation
between each of these variants and a given political trait.
I would argue that the next wave of genopolitics will be
focused on extending this earlier work in two related areas.
First, while knowledge that particular genes are correlated
with political traits is interesting, the causal pathways
linking the two are ultimately of more theoretical value.
Recent work suggests that personality traits, other-regarding
preferences, temporal discounting, attitudes towards risk,
and cognitive ability may mediate the relationship between
genes and political traits. However, most of these potential
mediators have yet to be formally tested and researchers
have had to rely on observational data in the few tests that
have been conducted. Yet, as Bullock, Green, and Ha (2010)
point out, mediation analysis using observational data is
likely to be biased (though see Imai et. al (working) for
discussion of new experimental design based approaches
and sensitivity analyses that may be of some help). While
experimental methods are not a panacea, they offer the best
opportunity to illuminate potential causal pathways.
The second expansion of the genopolitics literature will
be an explicit consideration of the ways in which genes and
the environment work together to influence political traits. A
limitation of the standard twin or association study designs
is that they tend to rely on an overly simplistic functional
form that assumes the influence of genes and environment
are additive and independent of one another. However, it is
more likely that genes and environmental factors combine
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interactively; our genetic endowment likely influences the
types of environmental settings we are exposed to either
because they influence which ones we seek out, or which are
imposed on us. The former scenario is known as
gene-environment interaction and the latter is known as
gene-environment correlation. A handful of published
political science studies have explored gene-environment
interactions; however, since they rely on observational data,
it is possible that exposure to the environmental factor being
studied is not truly exogenous but is due, at least in part, to
gene-environment correlation.
Field experiments offer an excellent way to disentangle
these two phenomena. For example, Jaime Settle, Peter
Loewen, and I found based on observational data that
individuals with a certain version of a gene previously found
to be associated with sensitivity to stressful stimuli were less
likely to vote when living in a more competitive political
environment, as compared to those with the alternative
variant. Our hypothesis was that a genetic predisposition to
stress sensitivity combined with a politically stressful
environment caused citizens to disengage from politics.
However, a problem with our research design was that
individuals sensitive to stress may choose to avoid living in
such environments. In order to overcome this problem, we
conducted a field experiment with Costas Panagopoulos in
the 2010 California election that randomly assigned a
mobilization message designed to elicit the type of stress we
hypothesized in the previous study helped cause
disengagement. The fact that the treatment was randomly
assigned, and could be compared to a control group, means
that the environmental influence was truly exogenous. While
this type of experiment has previously been done with
measures of personality traits, our study is an example of
how experimental methods can be used in the study of
genopolitics.
Political scientists have increasingly been granted access
to large genetically informative samples and are also actively
creating their own novel samples, making field experiments
even more feasible in the future. Recent work has also
conducted laboratory experiments on genetically informative
samples. In the foreseeable future, experiments will be the
norm in better understanding the causal relationship
between genes, the environment and political traits.
Alford, J., C. Funk and J. Hibbing. 2005. Are Political
Orientations Genetically Transmitted? American Political
Science Review 99(2):153167.
Bullock, John G., Donald P. Green, and Shang E. Ha.
2010. Yes, But Whats the Mechanism? (Dont Expect an Easy
Answer). Journal of Personality and Social Psychology 98
(April): 550-58.
Imai, Kosuke, Luke Keele, Dustin Tingley, and Teppei
Yamamoto. “Unpacking the Black Box: Learning about
Causal Mechanisms from Experimental and Observational
Studies.” Working paper available here
The Role of Protocol in the Design and
Reporting of Experiments
Thomas J. Leeper
Northwestern University
leeper@u.northwestern.edu
An average treatment effect is relatively simple to
estimate. The basic requirements of experimental research
that make that estimation straightforward and
unconfounded – manipulation of causal variables and
control over all else – are often far more difficult to achieve
than is often imagined or implied. In this article, I continue
the discussion started by Lupia and Druckman in the
inaugural issue of this newsletter by emphasizing how the
maintenance and publication of a detailed experimental
protocol is critical for the analysis and reporting of
experiments.
Developing Experimental Protocol
Like any novel data collection, an experiment is
complicated. It begins with research questions,
theory-building, and hypothesis generation. Experiments are
unique, however, in that these initial stages are followed by
a somewhat murky process of developing stimulus
(treatment) materials, disseminating those stimuli, and
assessing outcome measures. The idea of “just doing an
experiment” has probably occurred to many political
scientists – including non-experimentalists – but the process
of executing an experiment, and doing it well, is rarely a
topic heavily emphasized in published descriptions of
experiments. Executing an experiment well requires quality
protocol, by which I mean the detailed justification and
explanation of the experiment that will be implemented and
the record of how that intended experiment may not have
occurred, for what units, and why.
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A well-thought-out experimental protocol is the
experimenter’s version of the observationalist’s
well-thought-out statistical model of causes, outcomes, and
controls. Rosenbaum (2010) describes a “poorer
observational study”where “if sufficiently many analyses are
performed, something publishable will turn up sooner or
later.” This is not the way research – experimental or
observational – should be conducted. Instead, he offers that
“before beginning the actual experiment, a written protocol
describes the design, exclusion criteria, primary and
secondary outcomes, and proposed analyses” (7). Lupia
(2010) suggests that researchers record “Record all steps
that convert human energy and dollars into datapoints.”
Both quotes provide useful general advice, but the
experimental protocol should also includes many specific
features about the intended experiment, including:
Theory and Hypotheses
• Details of what outcome variable is under examination
(including the values of its potential outcomes) and
the causal factors (alone or in combination) that are
theorized to affect the outcome variable
• References to relevant prior designs (published or
unpublished) that inform the design, implementation,
and/or analysis of this experiment
• Exact listing of hypotheses with discussion of how each
hypothesis is reflected in one or more features
(manipulations or controls) of the intended design
• Discussion of how hypotheses were used to construct
the design (rather than design to construct
hypotheses), including how each hypothesis is testable
(i.e., falsifiable) in the intended design, including any
anticipated confounding between manipulated causes
and observed or unobservable alternative causes
Instrumentation
• Details of how theoretical constructs are manipulated
by the experimenter, including exact wording and
presentation of stimulus/treatment materials
• Details of how covariates and outcome variables are
measured and scaled and exact question wordings or
coding schemes if subjective and/or self-report
measures are used
• Explanation of how stimuli are predicted to affect only
the intended causal construct1
• Details of pretesting (of stimuli and/or outcome
measurement techniques) to validate whether stimuli
manipulate the causal constructs as anticipated by the
researcher, by manipulating only the intended cause, in
the theorized direction, and with what intensity
• Intended mode(s) in which each unit will be exposed
to each stimulus (e.g., in-person, via phone, internet,
mail, television, radio, print, etc.) and the mode in
which outcomes will be observed (e.g., in-person,
laboratory, internet, phone, voting records, etc.)
Population, Sample, and Treatment Assignment
• Details of sample construction, including how a
sampling frame was constructed of population units (if
applicable) and how units from that frame were
selected for or excluded from treatment assignment
• Details of randomization procedures, including how
random numbers were generated (whether a uniform
or some other probability distribution was used and
from where those numbers were obtained) and
assigned (across the entire sample, or within blocks,
clusters, or a combination thereof)
Implementation
• Intended (and executed) schedule for when, where,
and how treatments will be applied and outcome
variables measured and by whom (the experimenter or
an assistant, or a government agency, corporation,
etc.); if multiple sessions or repeated exposure to
stimuli are part of the design, the schedule should
specify and justify the order of what stimuli are applied
at each point in time
• Procedures for how units are made blind to their
treatment assignment, how data are collected and
stored regarding each unit prior to analysis, and how
1If experimenters are uncertain about how a given stimulus will alter the theoretical construct, pretesting should be conducted (as described). If a
stimulus potentially affects more than one causal construct (and alternative stimuli are infeasible), nonequivalent outcome measures – that measure the
desired construct and separately measure other causes that should be unaffected by stimuli – should be developed to demonstrate that the intended cause
produced the observed outcome and a confounding cause was not at work.
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anyone implementing the study are blind to each unit’s
treatment assignment and value(s) of outcome
variable(s) until analysis
• Details of manipulation checks and post-randomization
covariate balance tests, including how and when
manipulation checks will be administered and what
balance tests will be used and what predetermined
degree of imbalance will be considered problematic for
experimental inference
• Procedures for how deviations from protocol will be
recorded and utilized in data analysis, including errors
made by experimenters, item and unit noncompliance
or attrition, and other relevant notes
Analysis
• Definition of specific causal effects to be estimated for
testing each hypothesis; if more than two treatment
groups are implemented, this should include what
treatment groups or pooled treatment groups are used
to estimate those effects (i.e., specification of contrasts)
• Explanation of specific statistical analysis to be
performed, including how covariates will be used in
the analysis if at all (i.e., for regression,
subclassification, subgroup analysis, etc.)
• Plan for how to analytically address noncompliance,
attrition, missing data, or covariate imbalance
(through dropping observations, multiple imputation,
intent-to-treat analysis, etc.)
• Additional analyses or changes to this protocol should
be recorded in a “lab book”(Lupia 2010) and a record
should be kept of all analysis performed (in order to
reduce the risk of Type I errors)
In the same way that a regression model includes
putatively causal variables and “controls for” covariates and
confounds, the experimental protocol establishes what
factors vary between experimental units and what factors
are “controlled for” by uniform execution of the experiment
across randomized units. The protocol determines what
features (of subjects, of context, and of experimenters) are
included (observed and analyzed), excluded (unobserved),
or controlled for (observed or held constant across units) in
the final analysis, even if that analysis only consists of a
simple difference of means or difference of proportions test
for the average causal effect. Thinking about protocol forces
the experimenter to make and record decisions about what is
controlled in the experiment decisions that might otherwise
not be made, leading to unclear control or a loss of control
due to uneven implementation of the intended design.
Deviations from Protocol
The protocol should include description and justification
of all decisions regarding the intended experiment and
implemented experiment: i.e., if cost, feasibility, sample size,
time, ethics, or other constraints alter the intended
procedure, a record of these changes in the protocol
document (and the justification thereof) is the only way to
fully communicate what choices were made by
experimenters and why. Druckman (2010) noted that
experimental research is characterized by several myths; the
myth of experiments always working perfectly is probably a
necessary addition to his list; all experiments are – at some
level – broken experiments. The experimenter’s concern
needs to be placed on how to prevent, record, and
compensate for the deviations from protocol that manifest in
the implemented experiment. Compensating for deviations
that have already occurred is more difficult than preventing
them, but can only be done when deviations are anticipated
and properly recorded.
Rather than pretend that deviations from protocol do
not occur, researchers should keep the “lab book” called for
by Lupia to record statistical procedures, but they need to
also record the earlier unit-, treatment group-, and
sample-level deviations from the intended experiment
protocol before any statistical analysis is performed. These
deviations (especially if they correlate with treatment group
assignment) may undermine the elegance of experimental
inference by confounding causal factors and altering other
aspects of experimental control. At a minimum, if any
variations in implementation emerge among units, unit-level
variables should to be incorporated into the experimental
dataset that record:
• the date, time, and location that stimuli were
distributed or applied
• the date, time, and location that outcomes were
measured
• location and/or mode of each stage of the experiment
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
• waves of implementation, which place units in
different broader contexts even if procedures in each
wave are identical
• exogenous contextual events that influenced some
units but not others (due to timing of implementation,
geographical locale, etc.)
• any changes in questionnaires, changes in stimuli, or
changes in the contact between experimenter and
experimental units that affect only some units
• different experimenters/interviewers/coders/assistants
who administered stimuli, collected outcomes, or
coded data2
• other research-relevant, unit-level or group-level
deviations from protocol3
Reading a typical journal article, it would seem the types
of deviations from protocol included in the above list are
rarely seriously anticipated by researchers, considered in
data analysis, or honestly reported in publication. Dropping
observations and/or conducting intent-to-treat analysis are
common answers to deviations from protocol (often for
noncompliance, application of the incorrect treatment, or
attrition), but these are only applicable in some cases and
each may introduce bias into estimates of causal effects
depending on the type and extent of deviations. Other
answers certainly exist, but before we can address these
problems, we need to hold ourselves to high and uniform
standards of adopting, recording, and disseminating our
experimental protocols (see Gerber, Doherty, and Dowling
n.d.).
Reporting Protocol (and Deviations)
This level of full disclosure of experimental protocols is
relatively rare.4
While a journal article will often include a
brief discussion of protocol, specific details of protocol (and
deviations) are often omitted to save space or because those
details are seemingly unimportant (especially in the eyes of
non-experimenters). But, this is unfortunate and often
reflects, at best, partial compliance with standards for
reporting observational research. Druckman (2010) points
out “these standards [for surveys] do not ask for the
reporting of information critical to experimentation, such as
randomization checks, manipulation checks, pre-test results”
(10). Reporting on experiments requires more thorough
description in order for consumers of that research to
understand how the causal effect(s) might be constrained by
particular context, unit characteristics, poorly implemented
protocol, and so forth.5
Including the full protocol as an (online) appendix is
better than providing insufficient detail in an abbreviated
methods section. Reviewers would criticize a paper with
multiple statistical models if only one model were fully
described and would certainly take issue with analysis that
did not clearly specify the variables included in the analysis
and the rationale for controlling for or excluding particular
factors. Presenting a detailed experimental protocol is the
experimenter’s means of justifying relatively simple
statistical analyses. But an average treatment effect is not
just a difference in expected outcomes between groups; it is
a difference conditional on a large number of features of the
experimental design and broader context that are only clear
if they are considered, recorded, and explained by the
experimenter in the protocol document.
Seemingly similar experiments that yield different
effects estimates or substantive conclusions – think cold
fusion! – may be due to dissimilarities in protocol and
implementation that fail to be noted in lab books or reported
in published results. Experimental researchers need to
commit to incorporating deviations from protocol into their
final datasets, to sharing of those data, and to publication of
full protocols for the purposes of replication, meta-analysis,
and scholarly critique. Reproductions of stimuli, exact
questionnaires (or other outcome measurement tools), raw
datasets, statistical syntax files, and detailed protocols are all
necessary addenda to any published experiment.
Conclusion
2Demographic variables for these individuals may need to be included if they might influence unit behavior on sensitive issues (such as race or gender
for studies that examine those issues) or if data were gathered on each unit in systematically different (but unobserved or unobservable) ways.
3This could include units expressing anger or anxiety about the researcher’s intent in a study of emotions in politics, units communicating with other
units (which violates SUTVA), units that receive a treatment other than the one assigned or were exposed to more than one treatment, etc.
4Although social scientists rarely share their protocols, online sharing of protocols in the biological sciences is common at sites such as Nature Protocols
(http://www.nature.com/protocolexchange/) or SpringerProtocols (http://www.springerprotocols.com/).
5Given that experimental research enables meta-analytic review, thinking as a meta-analyst can also help researchers determine what protocol information
to report for a given study (see Lipsey 1994; Stock 1994).
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
The broad agenda of any experimental science is replication
and complication – the progressive addition of moderating
factors, search for mechanisms, and exploration of
alternative causes and outcomes. Writing and reporting
protocol is a critical best practice to establish strict
experimental control, to minimize noncompliance and
uneven implementation, to produce clear and accurate
presentation of results, and to properly interpret and
generalize experimental findings. Given the importance of
the (often unwritten) information contained within (often
unpublished) protocol to progressive scientific inquiry
(including replication and critique), we should not be afraid
of producing and sharing detailed records of our scientific
endeavors. But, more importantly, we should not forget the
importance of producing and enforcing protocol for
preserving the elegance of experimental inference.
References
Druckman, James N. 2010. “Experimental Myths.” The
Experimental Political Scientist 1(1): 9-11.
Gerber, Alan S., David Doherty, and Conor Dowling.
2009. “Developing a Checklist for Reporting the Design and
Results of Social Science Experiments.” Presented at
Experiments in Governance and Politics Network meeting,
Yale University, April 24-25, 2009.
Lipsey, Mark W. 1994. “Identifying Potentially
Interesting Variables and Analysis Opportunities.” In Harris
Cooper and Larry V. Hedges, eds., The Handbook of Research
Synthesis. New York: Russell Sage Foundation.
Lupia, Arthur. 2010. “Procedural Transparency,
Experiments and the Credibility of Political Science.” The
Experimental Political Scientist 1(1): 5-9.
Rosenbaum, Paul R. 2010. Design of Observational
Studies. New York: Springer.
Stock, William A. 1994. “Systematic Coding for Research
Synthesis.” In Harris Cooper and Larry V. Hedges, eds., The
Handbook of Research Synthesis. New York: Russell Sage
Foundation.
Review of FROM NATURE TO THE LAB:
EXPERIMENTAL POLITICAL SCIENCE AND
THE STUDY OF CAUSALITY
by Rebecca B. Morton and Kenneth C.
Williams
Sean Gailmard
Charles and Louise Travers Department of Political Science
University of California at Berkeley
gailmard@berkeley.edu
The experimental community in political science has
reached a level of self-awareness that seemed like a pipe
dream only a few years ago. Correspondingly,
experimentalists have confronted existential questions such
as, Where did we come from? How did we get here? What is
our purpose? And what are our sacred beliefs?
From Nature to the Lab covers all this ground in its
review of the study of causation, experimental methods, and
their intersection in empirical political science research. It is
an ambitious, and in my view, successful book. Morton and
Williams cover the theoretical link between experimentation
and causal inference; the issues of validity that scholars face
when using experimental and observational data; a wealth
of practical advice about the business end of conducting an
experiment (including a narrative “checklist” in the
appendix); and a wide range of research questions
addressed, experimental designs used, and results obtained
by experimentalists in political science over the years. The
book is conceptually and substantively rich but not
technically demanding. It should be accessible to first year
graduate students with one prior course on statistical
methods and inference; the text would easily occupy a
one-semester course on experimental methods. The book
will also be useful to practicing researchers new to
experimental methods, and enriching to seasoned
experimentalists.
Moreover, despite their pedigree in one of political
science’s several experimental traditions (namely, the game
theoretic/economic tradition), Morton and Williams are
self-consciously ecumenical in their coverage of issues and
literature from multiple traditions (namely, psychological as
well). This is not a book aimed at one “tribe” of
experimentalists, or at converting members from the other
tribe who have lost the true way. Rather, the book covers
theoretical and practical issues of common interest to all
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
experimentalists, as well as frankly reflecting a few points of
debate (e.g., subject incentives, deception).
The book is divided into three substantive sections. The
first covers the theory of causation in terms of the Rubin
causal model, the nature of experiments (which are defined
in terms of purposive manipulation of treatment variables),
prospects for control of confounding variables in
experimental and observational research designs, and what
the authors call the “formal theory approach” to causation.
One of the most important aspects of this manuscript is
that it thoroughly ties experimentation to problems of causal
inference in a comprehensive and systematic way. Given the
convergence of many social science disciplines on attention
to rigorous causal identification, and the folk wisdom that
experimentation is the gold standard of causal inference, this
link may seem natural or obvious. Yet this focus is either
lacking or implicit in many (especially early) political science
and economics discussions of experiments. Many early
experiments, especially in the game theoretic tradition, can
appear more as a sort of survey—what do real actually do in
a particular situation, and do they play subgame perfect
equilibrium strategies?—than an attempt to identify causal
effects of treatment variables. From a Rubin model
standpoint, for instance, it is not clear what causal effect is
established by the first ultimatum game experiments, or
experiments on any particular game in isolation.
A central premise of the book’s presentation on causal
inference is that there is no causal identification without
theory. In the sense that any model of causation, including
the Rubin causal model, makes theoretically contestable
claims about the meaning of causation, this is surely true.
But it does not follow that, having accepted the Rubin causal
model, additional substantive theorizing about the
relationship between treatment and outcome is necessary to
identify a causal effect in an experiment. Just as the
treatment effect of aspirin on headache pain was known
long before any coherent theory about the reason for this
effect was available, an experiment can identify the effect of
negative campaign advertising on interest in an election
without any particular psychological theory explaining the
effect. To be sure, such a theory would be useful to
determine which conceivable experiments would be worth
conducting, but that is a separate question from the one of
interpreting the effects of any given treatment in whatever
experimental data happens to be available.
Though From Nature to the Lab is explicit about its
connection of experimentation and causality, it does not
entirely accept the discipline’s convergence on the Rubin
causal model (RCM) as a touchstone of causation. This is
most apparent in chapter 6, “Formal Theory and Causality.”
Here Morton and Williams flesh out the “formal theory
approach” (FTA) to causality. They contend that the key
difference between the RCM and FTA approach to causal
inference in experiments is this: in the RCM approach, a
researcher assumes without proof that assumptions
underlying the causal prediction evaluated are consistent
with the assumptions underlying the method used to
evaluate them (p. 198); in FTA, a researcher “carefully
investigates whether each assumption for the theoretical
model holds for the empirical analysis and how these
assumptions matter in that analysis” (p. 202). This would
include, for instance, the assumption that the payoffs
instantiated in an experimental game match the utilities of
the relevant abstract representation (e.g. the extensive form
of that game).6
This is a high bar, and indeed it is not clear it is
attainable. How can a researcher ever be completely sure
that the subjects’ perception of a game coincides exactly with
the formal representation in the underlying theory? And if
we are not completely sure, how can the concordance of
actual behavior in a game as instantiated in an experiment
and equilibrium “predictions” be taken, in and of itself and
without comparison to any other game, to supply causal
information? Such a concordance seems inherently
vulnerable to arguments of confounding, from an RCM
standpoint. For instance, if an exceedingly complex game is
so inscrutable to subjects that they choose randomly (or
choose the first option offered, etc.), and this happens to
coincide with the equilibrium prediction in that game, what
can be inferred about the causal effect of the strategic
structure on actual behavior?
This very question, of course, assumes that the RCM
standard of causation can be used to evaluate causal claims
in the FTA framework. Morton and Williams do not attempt
to “square the circle” of reconciling the causal pretensions of
each approach within a single coherent theory of
6In Morton and Williams’s framework, experiments on formal theories may be couched in either an RCM or FTA framework; non-formal theories are consigned
to RCM frameworks only. This implicitly elevates the rhetorical powers of mathematics above mere verbal expressions of logic: the Morton-Williams
FTA framework implies that expressing the exact same logic of a formal model in verbal terms without the symbolic representation loses something.
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
causation—an interesting question for methodological
research, perhaps, and therefore an unreasonable goal for a
book of this nature. Instead, and consistent with the tenor of
the book more generally, they take each tradition on its own
terms and explore the logic of causal identification in
experiments within that tradition.
The second core section covers the theory of validity and
its implications for experimental and observational research
designs. Morton and Williams adhere faithfully to the
updated validity typology of Shadish, Cook, and Campbell
(2002). They provide a spirited argument against the
conventional view that experiments, while achieving
maximal internal validity, score lower on external validity
than observational designs. They maintain, instead, that
external validity is essentially an empirical question, and
thus anyone arguing against the external validity of
experimental designs must adduce evidence before this
conjecture can be accepted. Moreover, Morton and Williams
contend that one cannot logically analyze external validity of
experiments in situations where internal validity (including
statistical, causal, and construct validity) is not also satisfied.
Together, these empirical and logical arguments present a
nearly insurmountable burden for the hapless critic who
assails the generalizability of experimental findings.
Despite this argumentation, one supposes that the
critique of experiments in terms of a home-grown notion of
“external validity” will continue unabated, and therefore
experimentalists would do well to consider the verisimilitude
of the environments they create. In the end, Morton and
Williams are sanguine to this, and present analyses of
artificiality of experimental environments (including subject
pools and incentives) that experimentalists can draw on in
design and presentation of results.
The final substantive section addresses the ethics of
experimentation. This discussion covers both the history and
current content of standard codes of ethical conduct in
experiments, and also the issue of deception, one of the
principal points of contention between various experimental
traditions in political science (game theoretic vs.
psychological). This is arguably the area where Morton and
Williams get closest to advocacy of the norms of one
experimental tradition over another. Yet their presentation of
the costs and benefits of deception is quite even-handed, and
their call for a norm of minimal deception eminently
reasonable—particularly as pertains to institutions where
researchers from the two dominant traditions share a subject
pool.
Overall, From Nature to the Lab gives a comprehensive
overview of the theoretical benefits of, and theoretical and
practical issues involved in, conducting and analyzing data
from an experiment. It is at once a theoretical analysis of,
primer on conduct of, and review of literature from political
science experiments. Though the book certainly contains the
sorts of contestable claims that will make it interesting to
experimentalists and political methodologists, its judicious
treatment of an emerging canon of theoretical and practical
issues in experimentation will make it a standard text on the
topic for years.
Does Blocking Reduce Attrition Bias?
Thad Dunning
Department of Political Science, Yale University
thad.dunning@yale.edu
Several political scientists have recently drawn attention to the merits of blocking in experimental studies.
Experiments allow for unbiased estimation of average causal effects for the experimental study group, as long as
attrition and some other threats to internal validity do not arise. However, estimators may be more or less precise. This is
where blocking comes in. Here, units are grouped into strata, or blocks, and then randomized to treatment and control
conditions within these blocks.
For instance, experimental units may be grouped into pairs with similar incomes, past voting histories, or values of other
variables that may predict an outcome. In such “matched pair” designs, one member of each pair is randomly assigned to
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
treatment, while the other is randomly assigned to control.
As Moore (2010) and others have pointed out, blocking can be a worthwhile strategy, especially in smaller experiments.
Blocking is most beneficial when units are relatively homogenous (with respect to the outcome) within blocks and
heterogeneous across blocks. Thus, if investigators can identify variables that are good predictors of the outcome, blocking
units before randomization may increase the precision of treatment effect estimators.
Matched-Pair Designs and Attrition Bias
Yet, can blocking overcome bias from attrition or non-compliance? Following King et al. (2007), Moore (2010) suggests that
“Through blocking, design can anticipate and overcome a frequent field experiment reality: some units may be
compromised during an experiment, and they and their blockmates can be excluded from analysis without endangering the
entire randomization.”
Attrition occurs when some units are lost to follow-up—that is, when the outcomes for some units are not recorded, for
a variety of possible reasons. Such attrition can be devastating to causal inference when it is associated with treatment
assignment and is a function of potential outcomes (that is, the outcomes that we would observe for each unit if it were
assigned to treatment or control).
For example, the subjects most likely to drop out of a medical trial may be those assigned to treatment, for whom the
treatment does not appear to be working. In this case, comparing health outcomes of subjects who remain in the treatment
group to subjects assigned to control may overstate the efficacy of treatment, since subjects for whom the treatment did not
seem to work dropped out of the trial.
Similar issues can arise with non-compliance, which occurs when units assigned to treatment receive the control, or vice
versa. For instance, in randomized public policy programs, politicians may be tempted to administer the treatment to
control units (King et al. 2007). If we conduct analysis by treatment received—comparing those who receive the treatment
to those that receive the control—we risk bias. This is because units that crossover from control to treatment, or vice versa,
may be unlike those that don’t, in ways that matter for outcomes.7
Yet if attrition or non-compliance are functions of potential outcomes, dropping blocked pairs does not eliminate the
bias. To see this, imagine that there are two types in the experimental population:
(1) Units that will be compromised (e.g., be subject to attrition) if they are assigned to treatment; and
(2) Units that will not be compromised, whether assigned to treatment or control.
If subjects are randomized in pairs, and we throw out all the pairs in which the treatment unit is compromised, then we
know that all of the treatment units that are thrown out are of type (1).
Yet, the control units in the excluded pairs may include both types (1) and (2). For these control units, we don’t get to
observe the counterfactual response to treatment assignment—that is, whether the control unit would stay in the
experiment or not if assigned to treatment.
This can lead to bias, if the propensity to be compromised is related to potential outcomes, because the control group
contains types (1) and (2), while the treatment group contains only type (1).
A Numerical Example
A numerical example may help to illustrate this point. Suppose that in a small experiment, there are four units that will be
blocked on a single covariate and then randomized to treatment within blocked pairs.
The table below shows the covariate value for each unit; the potential outcome under control, which is denoted Y (0);
and the potential outcome under treatment, which is denoted Y (1). The final column records whether or not the unit will
be lost to attrition if assigned to treatment.
The final row of the table shows the mean outcome if all units were assigned to control and the mean outcome if all
units were assigned to treatment. The average causal effect is defined as the difference between these quantities.
7Non-compliance is typically not as harmful for inference as attrition: we can always do intention-to-treat analysis, which estimates the effect of treatment
assignment. There are also sensible procedures for estimating the effect of treatment on compliers, using treatment assignment as an instrumental variable.
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
Covariate value Y (0) Y (1) Lost to attrition if assigned to treatment?
2 1 2 NO
2 3 3 NO
3 4 6 YES
3 2 3 NO
Mean outcome: 10
4
14
4
Here, the true average causal effect is 14
4 − 10
4 = 1.
Now, suppose we randomize in pairs defined by values on the covariate: for instance, we flip a coin to decide which of
the two units with covariate value 2 goes into treatment, and similarly for the two units with covariate value 3.
This implies that there are 4 possible random assignments. The realized outcomes under each assignment are listed in
the tables below. The pairs that will be dropped due to attrition are indicated with diagonal slashes.
For each randomization, the estimated average causal effect—that is, the mean outcome in the treatment group minus
the mean outcome in the control group, after dropping the pairs in which there was attrition—is listed below each table.
Randomization 1
Covariate value Realized outcome Realized outcome
(control units) (treatment units)
2 2
2 3
¡3 ¡6
¡3 ¡2
Mean outcome: 3
1
2
1
Estimated average causal effect: 2 − 3 = −1
Randomization 2
Covariate value Realized outcome Realized outcome
(control units) (treatment units)
2 2
2 3
3 4
3 3
Mean outcome: 7
2
5
2
Estimated average causal effect: 5
2 − 7
2 = −1
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
Randomization 3
Covariate value Realized outcome Realized outcome
(control units) (treatment units)
2 1
2 3
3 4
3 3
Mean outcome: 5
2
6
2
Estimated average causal effect: 6
2 − 5
2 = 1
2
Randomization 4
Covariate value Realized outcome Realized outcome
(control units) (treatment units)
2 1
2 3
¡3 ¡6
¡3 ¡2
Mean outcome: 1
1
3
1
Estimated average causal effect: 3 − 1 = 2
The average estimated causal effect is the average over all of the estimates obtained after each of the 4 possible
randomizations, that is,
−1 − 1 + 1
2 + 2
4
=
1
8
.
This estimator is biased by about −88%, since the true average causal effect is 1. Thus, we have a substantial bias induced
by a relatively small association between potential outcomes and the propensity to be compromised. The logic carries
through to larger experiments and more complicated examples. For instance, one can construct illustrations in which the
average estimate of the average causal effect is negative, even though the individual causal effect is non-negative for every
unit and positive for many units.
Notice that dropping pairs in which one pair is subject to attrition also does not recover an unbiased estimate of the
causal effect for the first, second, and fourth units—that is, the units not subject to attrition. For these units, the average
causal effect is 8
3 − 6
3 = 2
3 , so the average estimate of 1
8 is quite a bit off. Whether the average causal effect defined only for
non-attriters is an interesting quantity is a different, perhaps substantive question. My point here is simply that randomizing
in pairs, and dropping pairs in which there is attrition, does not recover this effect, in this example and many others.
One can construct additional examples, in which there is a perfect correlation between blocked covariates and the
propensity to be subject to attrition if assigned to treatment; in such examples, the strategy of dropping pairs may give
unbiased estimates of the average causal effect, defined only for units not subject to attrition. In practice, however, this
strategy will depend on a strong assumption about unobservables: we have to assume that all units with the same values of
the blocked covariate respond similarly to treatment assignment. Yet, with just one randomization, we do not get to observe
the counterfactual response to treatment assignment of control units, that is, whether they would stay in the study if
assigned to treatment. So this supposition is not amenable to empirical evaluation.
Returning to the example above, notice that these problems go away if there is no attrition. Indeed, if we include all of
the outcomes in the calculations, the average of the four estimates equals 1, just as it should—because without attrition, the
difference of means is an unbiased estimator for the average causal effect.
Blocking Increases Efficiency; It Does Not Reduce Bias
It may be worth making one final clarifying point about the role of bias in small, unblocked experiments. As Moore (2010)
points out, one of the advantages of blocking is that it can reduce the chances that the treatment and control groups are
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unbalanced, at least on the blocked covariates. This is especially useful in small experiments, where the luck of the draw
implies that there may be substantial imbalances across treatment and control groups on measured covariates.
However, random imbalances that arise between treatment and control groups do not lead to confounding, in the
statistical sense—contrary to Moore’s (2010) claim that blocking “reduces the bias in causal estimates that comes from
comparing a treatment group [with covariate values] of 2, 2, 3 with a control group of 3, 4, 4.” It is true that in the data, on
any particular draw, covariates such as past voting history may be associated empirically with (realized) treatment
assignment. Yet, bias is not the issue here: randomization ensures balance on pre-treatment covariates, in expectation. The
issue is instead sampling error—that is, the random imbalances induced by random sampling of the treatment and control
groups from the experimental study group—which is a different concept.
In sum, blocking can increase statistical efficiency by balancing the treatment and control groups on blocked covariates,
but this is not a means of reducing bias.
Conclusion
Attrition can be quite destructive for experimental inference, when the propensity to be compromised or lost to follow-up is
associated with potential outcomes. It would therefore be useful to have a way to adjust this problem away.
Yet, it appears that blocking, and dropping pairs in which one of the pairs is compromised, does not get us around this
thorny problem. Blocking can be an effective tool to increase the precision of treatment effect estimators—but whether it
reduces bias depends on substantive assumptions that are not justified by randomization or other aspects of the
experimental design. Other strategies—for example, investing resources in tracking down units that are lost to follow up, or
just a random sample of those units (Geng et al. 2008)—may offer better alternatives for reducing attrition bias.
References
Geng, Elvin H., Nneka Emenyonu, Mwebesa Bosco Bwana, David V. Glidden, and Jeffrey N. Martin. 2008.
“Sampling-Based Approach to Determining Outcomes of Patients Lost to Follow-Up in Antiretroviral Therapy Scale-Up
Programs in Africa.” Journal of the American Medical Association 300(5): 506-507.
King, Gary, Emmanuela Gakidou, Nirmala Ravishankar, Ryan T. Moore, Jason Lakin, Manett Vargas, Martha Mara
T´ellez-Rojo, Juan Eugenio Hern´andez ´Avila, Mauricio Hern´andez ´Avila and H´ector Hern´andez Llamas. 2007. “A ‘Politically
Robust’ Experimental Design for Public Policy Evaluation, with Application to the Mexican Universal Health Insurance
Program.” Journal of Policy Analysis and Management 26(3): 479-509.
Moore, Ryan. 2010. “Blocking Political Science Experiments: Why, How, and Then What?” The Experimental Political
Scientist: Newsletter of the APSA Experimental Section 1(1): 3-5.
Blocking, Balance Testing, and Analysis with Optmatch and RItools8
Mark M. Fredrickson
Department of Political Science, University of Illinois at Urbana Champaign
mark.m.fredrickson@gmail.com
Often, when I write about the R packages Optmatch and RItools , I am showing how to use them on observational
data. For example, how to match observational data and test to see if the data appear balanced, as they would if they were
experimentally generated. These same techniques apply to the design and analysis of experimental research.
Pre-randomization blocking is matching. Reviewers and readers want demonstrations that treatment conditions are
balanced on covariates. Analyzing outcomes should respect the original design, including blocking.
This paper is a “how-to” guide for using Optmatch and RItools to implement these goals.9
It is written for the
researcher who thinks blocking and randomization based inference are the right tools for experimental research and would
like to see some example R code step-by-step. It is also for the researcher who is interested in adopting these techniques, but
8I thank Jake Bowers and Ben B. Hansen for their help throughout this paper.
9For more on the theory of blocking, see Wu and Hamada (2009) and Bowers (2010). For more on randomization inference, see Rosenbaum (2010).
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is concerned about added complexity. Hopefully, this tutorial demonstrates how easy it is to block and analyze experimental
data. After creating some data, I demonstrate how to create blocks of similar units, test for balance on covariates for blocked
and unblocked data, and test hypotheses of treatment effects. If you wish to extract this code or make changes, the original
source documents can be found at my GitHub page.
Data
Let us begin by creating some data in the style of the potential outcomes framework (Holland 1986). Let U be all
meaningful covariates related to the outcomes Yc and Yt. We observe X ⊂ U, but do not observe W ⊂ U. The covariates are
a mix of discrete and continuous random variables.
> n <- 100
> x1 <- rbinom(n, 10, 0.25)
> x2 <- rbinom(n, 1, 0.6)
> x3 <- rnorm(n, 50, 10)
> x4 <- rnorm(n, 0, 1)
> x5 <- runif(n, 0, 100)
> w1 <- rnorm(n, 0, 1)
> w2 <- rbinom(n, 1, 0.1)
> w3 <- runif(n, 0, 1)
> X <- data.frame(x1, x2, x3, x4, x5)
> W <- data.frame(w1, w2, w3)
The outcome Y is a continuous measure that is a function of the covariates and the treatment indicator. We first create
Yc from the covariates, and Yt is simply Yc + τ, where τ is the treatment effect. The function relating the covariates to the
outcome is arbitrary and only influences the analysis through the difference in potential outcomes.
> tau <- 10
> yc <- 0.25 * x1 + 4 * x2 + exp(x4) + x5 + 10 * w1 * w2 - w3 *
+ x3
> yt <- yc + tau
Blocking and Randomization
To implement blocking, we use the matching procedures in the Optmatch package for R. Optmatch implements a
procedure known as “optimal full matching” that minimizes the average distance between matched sets (Hansen and Klopfer
2006). Optmatch was designed with observational studies in mind, where the researcher has discovered “treatment” and
“control” groups. Optmatch will then find matches between similar treated and control units. This strategy is known as
“bipartite matching.” For more on matching (and using Optmatch in an observational study) see Rosenbaum 2010.10
In our situation, we do not have an existing randomization vector for our data, but we still wish to create similar subsets
of our data. Therefore we need to create the two partitions of the data that Optmatch will use. The most straightforward
way to create the splitting vector is to do so randomly. Just as with random assignment, in expectation these two groups
should not systematically different, allowing us to find a useful blocking scheme.
> s <- vector("logical", n)
> s[sample.int(n, n/2)] <- T
To create the blocks, we use the pairmatch function.11
We need to specify a distance matrix between observations,
10While the optimality guarantees of Optmatch are attractive, there are many alternative methods of blocking. See for example the blockTools package
and a walk through Moore 2010 in the previous issue of this newsletter.
11pairmatch will create matches with one observation from each random set. Optmatch allows tuning the number of observations allowed from each
random set. See the documentation fullmatch for more details.
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
and we can use the convenience function mdist to create a distance matrix based on the Mahalanobis distance between
observations.12
> blocks.all <- pairmatch(mdist(s ˜ x1 + x2 + x3 + x4 + x5, data = cbind(s,
+ X)))
For reasons of convenience or theoretical importance, we may wish to privilege certain variables and force the matching
within levels of those variables. For example, if units are clustered within a geographic unit — cities within a state — we can
limit matches to within the state. This is also a useful technique when matching large numbers of subjects (see my website
for more details on speeding up the matching process). To limit matches within blocks, we specify a factor indicating unit
membership. In our case, let use just match within the binary variable x2. Prior to doing so, we will create a new split that
places 50% of each treatment level in the partitions.
> count.x2.1 <- sum(x2)
> X.ordered <- X[order(x2), ]
> s.x2.0 <- sample.int((n - count.x2.1), (n - count.x2.1)/2)
> s.x2.1 <- sample.int(count.x2.1, count.x2.1/2)
> s.x2 <- vector("logical", n)
> s.x2[c(s.x2.0, s.x2.1 + (n - count.x2.1))] <- T
> blocks.x2 <- pairmatch(mdist(s ˜ x1 + x3 + x4 + x5 | x2, data = cbind(s = s.x2,
+ X.ordered)))
For simplicity, we will continue with the single stratum blocking, but splitting up matching problems into smaller blocks
is a very useful technique to have at your disposal.
Once we have blocks, we can then randomize within the blocks. As we used a pair-matching strategy, we will randomize
to two treatment levels, call them “treatment” and “control.” Since each observation is matched to one other we have 50
blocks with two units each. For each block, we can flip a coin and assign either the first or second unit to the treatment
condition.
> tmp <- rbinom(n/2, 1, p = 0.5)
> z <- vector("logical", n)
> for (i in 1:(n/2)) {
+ if (tmp[i] == 1) {
+ z[i * 2 - 1] <- T
+ }
+ else {
+ z[i * 2] <- T
+ }
+ }
As our last manipulation to the data, create a variable that is the observed outcome (Yc if z = 0 and Yt if z = 1).
> all.data <- cbind(X, z, b = blocks.all)
> all.data$y <- ifelse(z, yt, yc)
Balance Testing
In expectation, randomization balances covariates, observed and unobserved. In practice, a particular randomization
may place more men in treatment or more large towns in control. Experimental studies frequently provide a table of
12mdist accepts several different methods of specifying distances between observations, including a method that takes arbitrary functions. One could use
this method specify distance metrics that are more appropriate to your data if you have strong theory relating the covariates to the potential outcomes. See
the documentation for mdist for more information and examples.
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
Standardized Differences
q
q
q
q
q
0.00 0.05 0.10 0.15
x1
x2
x3
x4
x5 q blocked
Figure 1: Standardized differences of means for simulated data.
covariates, showing descriptive statistics for treatment and control, and perhaps a set of t-tests testing the null hypothesis
that the treatment and control units do not differ on each covariate.
Just as we might prefer an omnibus F-test to a series of t-tests in a regression, we might also prefer an omnibus test of
balance. Hansen and Bowers (2008) provide just such a test. Instead of checking each covariate individually, the test
compares all differences of means with a test statistic that converges to a χ2
distribution. This test is implemented in the
function xBalance in the package RItools .
The tool works with blocked or unblocked data. Using the blocks and treatment created in the previous section, Table 1
provides a summary of the balance testing. With a large p-value, we see little evidence that the data are not balanced (at
least when considering means).
> observed.balance <- xBalance(z ˜ x1 + x2 + x3 + x4 + x5, data = all.data,
+ strata = data.frame(blocked = all.data$b), report = "all")
chisquare df p.value
blocked 1.41 5.00 0.92
Table 1: Omnibus balance test of balance. The null hypothesis is that the data are balanced.
We might also be interested in the balance of individual covariates. Figure 1 shows individual differences of mean
(standardized) for the blocked balance assessments.13
None of the differences are very large (all less than a quarter
standard deviation’s difference). xBalance will report per-covariate tests of balance as well, but the with the results of the
omnibus test, we need not consider these.
Outcome Analysis
Figure 2 shows the treatment and control groups plotted on the outcome Y . We see a large degree of overlap in the
distributions. While the mean difference of the two groups properly captures the simulated treatment effect τ = 10, there is
a good deal of overlap between the two groups. What is the probability that difference is simply due to chance?
13This is the default plot method of xBalance objects.
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
y
Density
0.000
0.005
0.010
−50 0 50 100
q qqqqq q
q q qqq qqq qq
qqq qq q q
q
q
qqqq q qq q qqq q
qq
q
qq
q
q
q q q
qq
q qq q qq
qqq q qqq
q
q q q
q q
qq qq qqq qqq
q qq
q
q qqq qq q
q
q
q
qq qq q
qq
Figure 2: Outcome plot of treatment and control units
If we follow Fisher’s advice that randomization is the “reasoned basis for inference”, we will use a test that respects the
randomization in computing the likelihood of observing the differences we see between our treatment and control groups.
Two common randomization methods in R for computing a confidence interval for τ, the additive effect of treatment, are
the wilcox.test in the stats package and oneway test in the coin package. Sadly, neither of these functions
simultaneously support blocking and confidence intervals. Fortunately, we can adapt xBalance to provide block aware
point estimates and confidence intervals, using a Normal approximation to the randomization distribution. First we need to
write a function captures the range of values we wish to test as a confidence interval.14
> f <- function(low, high, step) {
+ adjustments <- seq(low, high, step)
+ ys <- paste("I(y - z * ", adjustments, ")")
+ as.formula(paste("z ˜", paste(ys, collapse = "+")))
+ }
For the data plotted in Figure 2, we can see that most of the mass is between -50 and 50, so we can test that range of
hypotheses. We ask xBalance to use our blocking factor and return p-values for each of the tested hypotheses. In effect,
we are inverting a series of hypothesis tests to generate a confidence interval.
> analysis <- xBalance(f(-50, 50, 0.5), data = all.data, strata = all.data$b,
+ report = c("z.scores", "p.values"))$results[, , 1][, 2]
> analysis.ci <- analysis[analysis > 0.05]
> analysis.ci.bounds <- c(analysis.ci[1], analysis.ci[length(analysis.ci)])
> print(analysis.ci.bounds)
I(y - z * 6) I(y - z * 31.5)
0.05140110 0.05710257
While the 95% confidence interval is rather wide at [6, 31.5], it properly rejects the null hypothesis of zero effect. Given
the size of the true effect compared to the variance of the data, this interval is actually quite tight. It is unlikely that an
unblocked design would find any difference.15
For a point estimate, we can use xBalance more directly.
14We are working at automating this process in future versions of RItools.
15While not reported here, a wilcox.test on an unblocked randomizations was unable to reject zero effect.
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
> xBalance(z ˜ y, data = all.data, strata = all.data$b, report = "adj.mean.diffs")
strata strat
stat adj.diff
vars
y 18.93530 **
While larger than the true effect, given the variance, the point estimate is not that far off.
Conclusion
In the introduction I noted that the these tools, while often used for observational research, are equally at home for
experimental work. I will now invert this statement to point out that the techniques in this tutorial are also useful for
observational research. A matching analysis attempts to block observations on observable covariates (perhaps reduced to a
propensity score). Testing balance is key to knowing if the matching achieved its goals. If we then allow the assumption that
the data are “as-if” randomized, the proper analysis draws upon the randomization and blocking. Optmatch and RItools
provide a set of tools that can be used for many types of analysis, both experimental and observational.
References
Bowers, J. (2010). Making effects manifest in randomized experiments. In Green, D. P., Kuklinski, J., and Druckman, J.,
editors, Handbook of Experimental Political Science. Cambridge University Press.
Hansen, B. B. and Bowers, J. (2008). Covariate balance in simple, stratified and clustered comparative studies.
Statistical Science, 23:219.
Hansen, B. B. and Klopfer, S. O. (2006). Optimal full matching and related designs via network flows. Journal of
Computational and Graphical Statistics, 15(3).
Holland, P. W. (1986). Statistics and causal inference. Journal of the American Statistical Association, 81(396):945–960.
Moore, R. T. (2010). Blocking political science experiments: Why, how, and then what? The Experimental Political
Scientist, 1(1):3 – 5.
Rosenbaum, P. R. (2010). Design of Observational Studies. Springer, New York.
Wu, C. F. J. and Hamada, M. S. (2009). Experiments: Planning, analysis, and optimization. Wiley and Sons, 2nd edition.
Section News and Announcements
• Update from APSA panel chair Kevin Arceneaux
APSA recently announced the preliminary program for the 2011 meeting (see below), and it has been a privilege to serve as
program chair for the newly minted Experimental Research Division. As a healthy sign of the growing interest in
experimental research, we received 115 paper proposals and 4 panel proposals on a diverse array of topics. Because this is
our inaugural year, the Association allotted us only three panels. Fortunately, it was possible to organize six panels by
arranging co-sponsorships with other divisions. In particular, the Formal Methods, Political Psychology, Political
Methodology, Comparative Politics, and Elections and Voting Divisions agreed to partner with us on panels that feature
cutting edge experimental research. I am also happy to report that a seventh panel, showcasing field experimental research
on the organization of political rights across three continents, was selected by the APSA Program Committee for a coveted
spot on the program as a Theme Panel.
Unfortunately, I was not able to find a home for many strong proposals. Although the large number of submissions is an
encouraging indicator that some of the discipline’s most promising research is employing experimental methods, it will
probably be little comfort for those who could not be included in the program. The only remedy here is for all of us to make
a strong showing in Seattle at the Division’s panels and, in so doing, earn a larger slice of the pie at the 2012 meeting.
APSA Experimental Section Officers
21
Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
• President: Jamie Druckman (2011)
• President-elect: Becky Morton (2011)
• At-large Council: Don Green (2011-2012), Mike Tomz (2010-2011), Lynn Vavreck (2010-2011)
• Treasurer: Kevin Estering (2010-2011)
• Secretary: Costas Panagopoulos (2010-2011)
• Newsletter editor: Dustin Tingley (2010-2011, renewable and appointed by President)
We are pleased to announce awards and policy committees. Awards are made possible through joining the APSA section.
• Best Dissertation in prior calendar year: Sean Gailmard (chair), Bethany Albertson, Nick Valentino, Shana Gadarian
• Best Paper at prior APSA: Josh Tucker (Chair), Rose McDermott, James Gibson, Eric Dickson
• Best Book: Ted Brader (chair), Susan Hyde, Maccartan Humphreys, Ismail White
• Junior scholars committee: Yanna Krupnikov (Chair), Rick Matland, Adam Levine, Chris Larimer, Samara Klar.
• Experimental standards committee: Alan Gerber (Chair), Kevin Arceneaux, Tom Palfrey, Cheryl Boudreau, Sunshine
Hillygus, Conor Dowling.
• New experimental political science journal: John Geer (chair), Rose McDermott, Don Green, Rick Wilson, Scott
Gartner, Dan Posner.
Recent Events
• Fourth Annual NYU-CESS Conference on Experimental Political Science
We are pleased to report that the NYU-CESS Conference on Experimental Political Science continues to go strong. The
4th Annual Conference was held March 4-5, 2011, and featured 15 paper presented and approximately 125 conference
participants. The conference aims to bring together political scientists united by their use of experiments in their research,
but without the normal sub-field boundaries that sometimes divide us. This year was no exception, with papers featuring
survey experiments, lab experiments, field experiments, and experimental methodology on the program. Participants came
from universities around the country and throughout Europe, and the conference was also bolstered by an excellent group
of discussants. This was the first time we had solicited discussants though the application process as well, and this worked
so well that we intend to continue it in the future. Additionally, this year’s program included a themed panel Friday
afternoon on experiments related to corruption. This also worked well, so we will certainly be open to considering another
themed panel next year.
• First Southern Political Science mini-conference on experiments
January 5-8, 2011, New Orleans, Sponsored by the APSA Experimental Research Organized Section this mini-conference
brought together papers by Rebecca Morton and Jean-Robert Tyran, Kevin Arceneaux and Martin Johnson, William Minozzi
and Jonathan Woon, Christopher Mann, Rick Wilson and Catherine Eckel, Dan Myers and Dustin Tingley, Ngoc Phan, Cindy
Rugeley and Gregg Murray, Laura Paler, Noam Lupu, and Brad LeVeck. The conferences promises to be exciting!
• Vanderbilt Lab Experiment Meeting
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
From May 4-May 6, Vanderbilt University hosted a small Conference on Laboratory Experiments in Political Science.
About twenty researchers from over a dozen universities met for two purposes: first, to discuss the creation of a Consortium
for Laboratory Experiments in Political Science, and second, to share innovative work based on laboratory experiments. The
Consortium for Laboratory Experiments in Political Science will serve as a clearinghouse for information about laboratory
experimentation. It will compile descriptions of participating experimental labs, with the purpose of facilitating
conversations and collaborations across labs. It will also provide a springboard for participating researchers to investigate
the possibility of trading subjects and time with researchers at other experimental laboratories. Such trades would enhance
the external generalizability of laboratory studies, by providing researchers with access to additional subject pools and
opportunities to field replications or extensions of projects. In addition to discussing the Consortium, researchers also
presented papers that focused on experimental design, multiple agent processes, implicit and automatic attitudes,
cue-taking, and biology. For more information about the Consortium for Laboratory Experiments in Political Science, contact
Cindy Kam: cindy.d.kam@vanderbilt.edu.
• WCE.2011, Caltech
The fourth annual meeting of the West Coast Experiments Conference (WCE) was held on the campus of The California
Institute of Technology on Friday, May 6.
Held each year in May, the WCE is a single day meeting that focuses on new methods for experimental research. The
WCE conference is organized as a methods ”workshop” than as a venue to engage in theoretical debate. Instead of standard
conference presentations, presenters focus in depth on one or two methodological take away points of their experimental
work. The goal is to give the audience members applied, practical advice on methods and design in a way that will help
them improve their own experimental research. We always encourage anyone with an interest in experiments to attend;
graduate students are especially welcome, as well as those who are new to experimental research.
We organized this years conference around two broad themes, one for the morning and one for the afternoon. The
morning panels were focused largely on design and analysis for causal inference. At the first panel, Susan Hyde (Yale
Political Science) and Craig McIntosh (UCSD School of International Relations and Pacific Studies) each presented on field
experimental research conducted in developing countries, Nicaragua for Hyde and Malawi for McIntosh, settings that often
present great challenges for designing and implementing studies that can identify causal effects. At the second panel,
Kosuke Imai (Princeton Politics) presented a new statistical method for analyzing data from an endorsement experiment to
identify support for militant groups in Pakistan.
At lunch Thomas Palfrey (Caltech Economics and Political Science) gave a keynote speech summarizing research he has
conducted over decades in various settings such as elections and juries, showing where Nash equilibrium predictions are
robustly supported across experiments, and where they are not. Palfreys bottom line is that Nash expectations can explain a
considerable amount of political behavior, but that there seems to remain a residual of behavior that requires other
psychological explanations such as heuristics or risk neglect.
Palfreys keynote speech nicely foreshadowed the afternoon panels, which were designed to offer a contrast between
experimental approaches adopted by those working in the economic tradition and those working in the psychological
tradition. In the first afternoon panel, Becky Morton (NYU Politics) and Erik Snowberg (Caltech Political Economy)
represented the economics tradition. Morton presented lab experiments designed to test whether participants vote to
express preference for a candidate or whether they vote with an eye to how a legislative assembly is finally constituted.
Snowberg presented a theoretical paper that framed subjects participation in an experiment as a principal-agent problem, a
framework that can identify not only treatment effects but also subjects beliefs about the effectiveness of the treatment itself.
The second afternoon panel focused on psychological approaches. Shana Gadarian (UC-Berkeley Public Health)
outlined new methods for eliciting anxiety in lab experiments, methods that can be embedded in experiments to test the
effects of anxiety on political participation, information gathering, and attitudes. Wendy Wood (USC Psychology) presented
a study that demonstrated the habitual nature of voting within a laboratory setting.
There were about 60 participants in all at the conference. The conference was a great success: the presentations were
informative and the audience was quite active in the discussions. Caltech was a gracious host and served as a magnificent
venue for the conference.
We expect to begin organizing WCE.2012 in the coming months. We will announce plans for next years conference in a
subsequent newsletter.
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Newsletter of the APSA Experimental Section 2011 Volume 2 Issue 1
Kevin Esterling, Nick Weller, Mat McCubbins, Jonathan Katz
Upcoming Events
• Fifth Annual NYU-CESS Conference on Experimental Political Science call for papers
Please mark your calendars for next year’s conference, which will take place on March 2-3, 2012. Joshua Tucker and Eric
Dickson will be co-directing the conference, and we expect to post a call for papers early in the fall. Thanks to the generosity
of NYU’s Department of Politics and the NYU’s Center for Experimental Social Science we continue to be able to offer the
conference without a registration fee and to provide free food throughout the weekend, so we hope to see as many of you
there as possible!
• 2011 APSA Annual Meeting
Lots of great section sponsored and co-sponsored panels! Room assignments pending.
Section 51: Experimental Research
51-1 Formal Models and Experiments: the New Frontiers, Thursday, Sep 1, 2011, 10:15 AM-12:00 PM
51-2 How People Think and Deliberate About Politics, Friday, Sep 2, 2011, 4:15 PM-6:00 PM
51-3 The Impact of Transparency on Government Performance: Comparative Evidence from Field Experiments, Sunday,
Sep 4, 2011, 8:00 AM-9:45 AM
51-4 Experiments on Cue-taking, Myopia, and Rationality, Thursday, Sep 1, 2011, 2:00 PM-3:45 PM
51-5 Experiments on Social Pressure and Mobilization, Thursday, Sep 1, 2011, 8:00 AM-9:45 AM
51-6 Methodological Issues in Randomized Experiments, Saturday, Sep 3, 2011, 4:15 PM-6:00 PM
51-7 Theme Panel: Organizing for Rights in Africa, Asia, and the Southwest: Field Experiments in Heterogeneous
Communities, Friday, Sep 2, 2011, 8:00 AM-9:45 AM
Back to Contents
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