Question 1. Two parallel flocculation basins are to be used to tre.docx

Question 1. Two parallel flocculation basins are to be used to
treat water flow of 150m3/s. If the design detention time is
20minute, what is the volume of each tank? If the average
velocity gradient in these two tanks is 124/s, calculate the
velocity gradient is each basin if the gradient in second basin is
half of the first one.
Question 2. Determine the volume of the aeration tank for the
following operating conditions:
Influent BOD5 concentration after the primary is = 150mg/L
Wastewater flow rate = 10MGD
F/M ratio = 0.2/d
Mixed Liquor volatile suspended solid concentration =
2200mg/L
Question 3. Given below is the wastewater characteristics,
determine the F/M ratio? (10 Points)
Influent BOD5 concentration = 84mg/L
Wastewater flow rate = 0.150m3/s
Volume of the aeration tanks = 970m3
Mixed Liquor volatile suspended solid concentration =
2000mg/L
Question 4. What is the terminal settling velocity of a particle
with a specific gravity of 1.4 and a diameter of 0.010mm in
20oC water? Would this particle be completely removed in a
settling basin with a width of 10.0m, depth of 3.0m, a length of
30.0m, and a flow rate of 7500m3/d? What is the smallest
diameter particle of specific gravity 1.4 that would be removed
in the sedimentation basin described above?
Question 5. Will grit particle with a radius of 0.04mm and a
specific gravity of 2.65 be collected in a horizontal grit chamber
that is 13.5m in length if the average grit-chamber flow is
0.15m3/s, the width of the chamber is 0.56m, and the horizontal
velocity is 0.25m/s? The wastewater temperature is 22oC.

Question 6. Wastewater treatment plant flow rate is 20MGD.
Chlorine dosage is 10mg/L. Determine chlorine requirement
(lb/day)
Question 7. If a particle having a 0.0170-cm radius and density
of 1.95g/cm3 is allowed to fall into quiescent water having a
temperature of 4oC, what will be the terminal settling velocity?
Assume the density of water = 1000kg/m3. Assume Stoke’s law
applies?
Question 8. If the terminal settling velocity of a particle falling
in quiescent water having a temperature of 15oC is 0.0950cm/s,
what is its diameter? Assume a particle density of 2.05g/cm3
and density of water equal to 1000kg/m3.
µ@15oC = 1.139 mPa-s
ρ @15oC = 999.103kg/m3
Question 9. Determine the diameter of a single-stage rock media
filter to reduce an applied BOD5 of 125mg/L to 25mg/L. Use a
flow rate of 0.14m3/s, a recirculation ratio of 12.0 and a filter
depth of 1.83m. Assume the NRC equations apply and that the
wastewater temperature is 20oC?
Question 10. Bacterial kill rate typically follows Chick’s law. If
the first-order kill rate for a certain weak disinfectant is
0.067/h. Determine the time it will take to reduce the bacterial
population to half of its original concentration?
Question 11. A town discharges 17,360 m3/d of treated
wastewater into the Creek. The Creek has a flow rate of
0.43m3/s and the DO of the creek is 6.5 mg/L and DO of the
wastewater is 1.0 mg/L. Compute the DO?
Question 12. The reaction for a biologically degraded
contaminant is first order. The half-life of the contaminant is 3
week. Determine the degradation rate?
Question 13. A sewage lagoon that has a surface area of 10 ha
and a depth of 1 m is receiving 8640 m3/d of sewage containing
100 mg/L of biodegradable contaminant. At steady state, the
effluent from the lagoon must not exceed 20 mg/L of
biodegradable contaminant. Assuming the lagoon is well mixed
and that there are no losses or gains of water in the lagoon other

than the sewage input, what biodegradation reaction rate
coefficient must be achieved for a first-order reaction
Question 14. A colony of bacteria exhibit exponential growth
behavior. If the number of bacteria doubles in 3 hours, how long
will it take for the size of the colony to triple?
Question 15. A sample of diluted wastewater (diluted 10 times)
has a 5 – day BOD of 5 mg/L. If the rate constant is 0.1/d,
determine the ultimate BOD of the original wastewater?
Question 16.
Question 17. The rate of reaction for an enzyme- catalyzed
substrate in a batch reactor can be described by the following
relationship:
where k = maximum reaction rate; mg/ L min C= substrate
concentration, mg/ L; K = constant, mg/ L
Using this rate expression, derive an equation that can be used
to predict the reduction of substrate concentration with time in a
batch reactor. If k equals 40 mg/ L.min and K= 100 mg/ L,
determine the time required to decrease the substrate
concentration from 1000 to 100 mg/ L.
C
K
kC
r
c
+
=
65
DESIGNING AN EXPERIMENT

To understand these different designs, I will start with the
process of designing an
experiment. Experiments are intended to explore cause-and-
effect relationships. Sup-
pose researchers want to determine whether a relatively
inexpensive organic fertilizer
is effective in increasing the crop yield of corn. Researchers can
create two separate
growing areas in a greenhouse and randomly assign the corn
seeds to the test area with
the organic fertilizer and to another area without it. Both areas
receive the same soil,
temperature, sunlight, and water. The scientists thus control for
all the key variables
so that the only difference between the two areas is the organic
fertilizer. The yields
are measured when the corn is harvested. If the test area with
the organic fertilizer
ha~ a higher yield of corn than the comparison area without the
fertilizer, then the
'-Cientists will conclude that the organic fertilizer made the
difference.
But what happens if the research is conducted in the field
instead of the controlled
en ironment of the greenhouse? If the two areas are close
together, the fertilizer might
run off into the comparison area, thus giving an imperfect
measure of the impact of
the fertilizer. The researchers might move the comparison area
to a different part of
the field to avoid run-off, but then the soil, light, temperature,
and/or rain may be
,Jightly different. Even if the corn yield with the organic
fertilizer is higher than the

corn yield without it, whether the fertilizer alone caused the
differences in the yield
, ' not absolutely clear.
Clearly, working in the field does not give researchers as much
control as they have
m the greenhouse, making it more challenging to conclude that
a cause-and-effect
~e lationship exists. Similarly, because public administration
research often takes place
··in the field'' rather than a laboratory, it is difficult to control
everything .
. A.=FILYING THE DESIGN ELEMENTS: THE Xs AND OS
fRAMEWORK
Researchers design their studies using various combinations of
the design elements.
hi le they may prefer to use specific elements, the situation
constrains their choices.
s~•metime the researchers can use before-and-after measures,
sometimes they can use
many measures before and after, and sometimes they can use
only a single measure
;.1thered after the program is implemented. Similarly,
sometimes they have a com-
::-arison group and sometimes they do not. I call this very
narrow concept of research
Jesign the Xs and Osframework because of the particular
notation used as shorthand
~,,Jr describing the design elements:
.Y is the causal factor, program, or treatment (you might think
of this as the indepen-
dent variable).

n is the observation or the measure of the effect (you might
think of this as the
measure of the dependent variable).
To understand the different ways these design elements can be
applied and their
limitations, let us walk through the design options available to
determine the impact
of a stress reduction program in an organization. I will present
them using the non-
experimental, quasi-experimentaL and experimental categories.
66
NONEXPERIMENTAL DESIGN
The human resources director asks for volunteers to participate
in a stress reduction
program and accepts the first fifty employees who raise their
hand. At the end of three
months, they are given a stress test to measure whether the
program was successful
in reducing stress. This one-shot design is the simplest, and the
notation looks like
this: ·
X 0
(the stress reduction program) (observation or measurement: the
stress test)
If the researchers find that the majority (75 percent) of the
participants have low
stress tests after the program, can the human resources director
claim that the program

is a success? Although she may make the claim, it lacks
credibility because too many
other factors might actually explain the observed results. Maybe
the fifty participants
were longtime meditation gurus. so their stress levels were
already low. Without a
baseline-a measure taken before the program began-it is hard to
say whether the
program actually changed the participants' stress levels.
To fix that, the researchers might opt to use a before-and-after
design, if it is pos-
sible. They administer a stress test to the participants before
starting the program ( 0 1 ):
this is the pretest or the baseline measure. At the end of three
months in the program,
they readminister the stress test (0:): this is the posttest. The
notation would look
like this:
01 X o,
(stress test) (the program) (stress test)
Have the stress levels changed? Suppose the researchers find
that stress levels in
the posttest are lower than they were before the program started.
Does that mean the
program was successful? Maybe. However, rival explanations
might exist to explain
the observed drop in the stress tests. Perhaps the agency's
stress-provoking director
left the organization during the first month of the program and
that really explains
the lower stress levels observed in the posttest.
To control for this, the researchers could choose to use a

comparison group of
employees who do not participate in the program but who take
the same stress test
as the participants three months after the program begins. This
is called a static group
design, and the notation would look like this:
Program participants
Comparison group
X 0
0
Perhaps the researchers find little difference between the
groups. Did the program
fail? Maybe. But it is also possible that the compari~on group
learned about the stress
reduction techniques from people in the program and began
using the techniques on
their own. Alternatively, they may have already been u.;ing
various stress reduction
_-:::: ~-·.::: --~ .... _ --~ - 67
~c~ 1mques. While the temptation would be to conclude that the
program did not work.
the reality is that the researchers do not know.
These three designs, which are called nonexperimental designs,
share a weakness
in being unable to control very much. Nonexperimental designs
are perfectly fine to
answer descriptive and normative questions. Sometimes
researchers just want to take

a snapshot of a situation at one point in time. For example. what
do citizens say are
the most pressing problems facing the city right now? This is
just a snapshot at one
point in time. The researchers may compare responses of people
based on income,
educational level, or neighborhood using statistical analysis of
data; this is often just
descriptive infonnation. Other times. however. researchers will
use statistical controls to
demonstrate causal relationships. Therefore, sophisticated users
of research results will
look very carefully at the intention of the research to detem1ine
whether the researchers
want to simply describe a situation or demonstrate a cause-and-
effect relationship.
Nonexperimental designs. however. are the weakest for
answering cause-and-
effect questions because they cannot do much to eliminate rival
explanations. That
said, sometimes researchers find that no other design option is
available given the
particular situation. As a general rule, sophisticated users of
research results should be
very cautious in making firm conclusions or policy decisions
when a nonexperimental
design is used to answer a cause-and-effect question.
QUASI-EXPERIMENTAL DESIGN
Using more of the design elements will increase the strength of
the design by giving
the researchers more ability to rule out rival explanations. As a
group, these designs
are categorized as quasi-experimental because they have some

but not all the features
of a true experiment.
One type of quasi-experimental design is to expand the before-
and-after design
by taking several periodic measures instead of just a single
postmeasure; generically,
this is called a longitudinal design. For example, the researchers
could extend the
program for nine months and take stress measures every three
months. While there
might be an initial drop after the stress-provoking director
leaves, what happens over
time? This design is likely to moderate the effect of the
departure of the director. The
notation would look like this:
oh~.·r(lft' X 0_7..month" oh month<; 09 month<;
However, this design does not eliminate all other possible
explanations. A major
problem is that these volunteers might be unique. Perhaps they
are highly motivated
to reduce stress and do other stress reduction activities outside
of work. Would this
program work for those not so motivated? That is unknown
based on this design.
If the researchers combine a comparison group with a before-
and-after design, they
will have a nonequivalent comparison design. This is noted:
Program group
Comparison group
X

68 CHAPTER 5
In this design, both the participants and the comparison group
(also called a control
group) take a stress test before the program begins. The
participants then engage in
the program while the comparison group does not. At the end of
three months, both
groups take another stress test. The changes between the before-
and-after measures
of the program participants are compared to the changes in the
comparison.group.
This design controls for events such as the departure of the
agency's stress-provok-
ing director. If the stress level declines are still greater among
program participants
than in the comparison group, we would be more willing to give
the program credit
for at least some of the reduction.
These groups, however, are not exactly the same (hence the
name nonequivalent),
so it is still possible that something about the groups themselves
affects the results
rather than the program. For example, suppose both groups are
interested in stress
reduction and actively meditate outside of the program. The
research might not,
therefore, show much change no matter how good the program
is because both these
groups were already at the lowest point in terms of the stress
test. In this scenario,

the program would appear not to work.
What else can the researchers do to design a stronger study?
CLASSIC EXPERIMENTAL DESIGN
The researchers can choose the third design element: random
assignment. By adding
it to the nonequivalent design, the researchers now have a
classic experimental design
(sometimes called a "clinical study"), which randomly assigns
people to the stress
program and the control group. This is noted:
Random assignment
Random assignment
Program group
Control group
X
Random assignment makes the groups comparable by
distributing a range of dif-
ferences to both groups. The health nuts, meditation gurus,
workaholics, and couch
potatoes are randomly assigned to the program or control group.
Neither group is
dominated by one type of person. Given the relative equality of
the groups, there-
searcher can feel confident in concluding that the program had
an impact if the pro-
gram participants show a substantial reduction in stress as
compared to the control
group. If, however, there was no difference between the groups,
the researchers can

feel confident in concluding that the program had no impact.
It should be noted that I am presenting a simple version of the
classic experimental
design here. Depending on the exact nature of the research,
experimental designs can
be very elaborate. For example, they can be designed so that the
participants do not
know if they are in the treatment or the control group (called a
single-blind study),
and sometimes neither the researchers nor the participants know
(called a double-blind
study). It is also possible to have multiple treatments (see
Application 5.1 ).
In studies testing medications, for example, the people in the
control group might
be given sugar pills to control for the "placebo effect."
Researchers have found that
the belief that taking a pill will make them better causes some
people to get better. So
DESIGNS FOR RESEARCH
Application 5.1
Treating Depression
An Experiment
Robert Whitaker describes several clinical studies that looked at
various treatments fo'r de-
pression and mental illness in his book Anatomy of an Epidemic
(201 0). One study compared
the impact of three modalities in treating depression:

medication, medication plus exercise,
or exercise alone (Blumenthal and Babyak, 2000). Participants
in the study were volunteers
aged fifty years and older who met DSM-IV criteria for major
depressive disorder and were not
taking any medications or self-medicating (alcohol. illegal
drugs). One hundred and fifty-six
people who met their research criteria were randomly assigned
to one of the three groups for
four months and were then tracked for an additional six months.
While the antidepressants did well in reducing symptoms in the
short term for the people in
those groups, those people were also more likely to relapse (30
percent in the drug and drug
with exercise groups, as compared to 8 percent in the exercise
only group). At the end of the
ten months, about 50 percent of the participants in the drug and
drug with exercise groups
reported symptoms, as compared to 30 percent of the exercise
only group.
Dr. James Blumenthal, one of the researchers for this study, told
the Associated Press
(Dreyfuss 2000), "The studies do not prove exercise relieves
depression, in part because the
exercisers worked out in a group, so group dynamics may have
played a role."
This is how science works. Even with a strong experimental
design, it is still possible that
other factors (rival explanations) might affect the results. More
research is needed.
69

everyone receives pills and no one knows whether it is the real
medication or a sugar
pill. Sometimes the placebo will mimic some of the possible
side effects, making it
harder for people to guess accurately which pills they have
received. If a substantially
greater percent of the people in the treatment group get better as
compared to the
control group, the placebo effect has been eliminated as a rival
explanation.
While the classic experimental design is the strongest in ruling
out other rival
explanations, random assignment in public administration
research may not be pos-
sible due to ethicaL legal, equity, practical, or political
constraints within a particular
situation. Clinical trials to test the efficacy of various drugs, for
example, might raise
ethical issues. Is it ethical to assign some people into an
experimental group that gets
treatment that may increase life expectancy and assign others
into a control group that
gets a placebo? In this situation, rather than use a placebo
researchers might either
test various dosages of the potential life-saving drug or test
similar medications.
There may be legal constraints that prevent random assignment.
It is not legal for
an employer to force people to participate in an experiment,
even one like the stress
reduction program. It is also illegal to deny people public
programs or benefits to
which they are entitled by law, such as food stamps, training
program for disabled

veterans, or unemployment benefits; this means that people
cannot be forced to par-
ticipate in a nutrition experiment, for example, under the threat
of losing their food
stamps. Equity may also be a constraint. Are the choices about
who gets to participate
fair, especially if participation provides a benefit?
Sometimes random assignment is simply impractical. It is
unlikely, for example, that
70 :::-:.:-::~ 5
Congress would randomly assign some states to a program and
other-. to a .:omparison
group that does not get the program. When laws are
implemented in every county or
every state at the same time, there is no way to form comparison
groups.
Random assignment might also pose a challenge to political
deal making. For
example, it is difficult to randomly assign cities to receive a
program that will bring
in millions of dollars from the federal government. Elected
officials from other cities
are likely to negotiate to have their cities included in the
experiment. As a result, the
cities are no longer randomly assigned (because political
influence has gotten them
included) and the pot of money might be divided up to the point
where it is insuf-
ficient to be effective in any city.

There may be situations, however, when an experimental design
can be used. For
example, when a program is not large enough to accommodate
all those who apply,
random assignment is possible (see Application 5.2 on pages
72-73 ). Since relatively
few can participate. random assignment not only provides a
strong design, it is also
more equitable because it rules out bias and favoritism in
selection. In the mid-1980s,
for example, a public-private partnership funded a huge
evaluation of welfare training
programs (Gueron 1988). Eight states were selected, and over
35,000 people who
volunteered to participate in the training program were
randomly assigned to one of
three groups: the full training program, a program with limited
job search services, or
the no-service control group. In states with a typical
unemployment rate, the programs
worked: those who participated in the full training program
earned more than those
who did not although the differences were generally small. This
is a good example
of how an experimental design can be used in the public sector.
DESIGN VARIATIONS
Every situation is different and therefore constrains the ability
to use one or more of
the design elements. In some situations, random assignment is
possible but there is
no way to get a preprogram measure. For example, suppose
researchers are testing a
training program for people on welfare. The researchers go
through the welfare rolls

in their town and randomly assign clients to the training
program or not. The outcome
measure is whether they get jobs and keep them for six months.
Since they are on
welfare when the program begins, there is no premeasure. Some
people may have
had prior work experience, but random assignment equalizes the
groups since people
with and without prior work experience are in both groups. My
point, however, is
that there will be no premeasure in this experimental design.
The notation using Xs and Os would look like this:
Random assignment
Random assignment
Training program
Comparison group
X 0
0
Sometimes researchers stumble on a situation that is naturally a
quasi-experimental
design. For example, until Indiana's state legislature decided to
put the entire state
on daylight saving time in 2006, only fifteen of its ninety-two
counties turned their
clocks forward in the spring and back in the fall (Lahart 2008).
This created a natural
DESIGNS FOR RESEARCH 71

experiment by which the energy use in the counties could be
compared. Using data
from monthly meter readings for three years, researchers were
able to compare energy
use before and after daylight saving went into effect as well as
compare the usage of
residents living in counties that were using daylight saving
before 2006 with those
who were not. The result? The researchers concluded that
daylight saving time does
not save energy or money: residential energy usage increased
between 1 percent and
4 percent, amounting to an additional $8.6 million a year that
consumers paid.
Another quasi-experimental variation is to find a group that is
matched on key
characteristics. Researchers might, for example. select two
schools that share very
similar demographic characteristics to compare a specific
program offered in one
school but not the other. The assumption is that if the
demographics are the same,
the schools are relatively comparable, so any observed
difference is likely to be due
to the program.
USING STATISTICAL CONTROLS TO CREATE
COMPARISON GROUPS
Creating comparison groups by using statistical controls is
another very common
quasi-experimental design. In the jargon, this type of design is
typically called cor-
relational with statistical controls, but variations are called an
ex post facto or causal

comparative design. Basically, they use analytical techniques
utilizing computer
software to make comparisons.
Suppose researchers want to determine whether the Head Start
program has a last-
ing impact on the reading abilities of the children who
participate in the program.
Assuming the data is available in school records, the
researchers design a study to
gather information on all the eighth graders in an inner-city
school district. This data
includes whether or not they attended Head Start, various test
scores, grades, and
demographic information.
Using statistical software. the researchers separate the students
into two groups:
those who attended Head Start and those who did not. The
software then performs
various statistics procedures to determine whether there is a
noticeable difference
in reading scores between the former Head Start and the non-
Head Start students.
Specifically how this is done will be presented in the analysis
chapters.
What else might affect a child's reading scores? Maybe the
educational level of the
mother, family income, or having attended nursery school
makes a difference. If these
data are included in the files, they can be used to test the
possible rival explanations,
and the researchers use statistical controls to examine reading
scores associated with
these factors. The computer software sets up comparison

groups. For example, the
computer can look at reading scores for children who attended
nursery school, Head
Start, or those who did not attend any type of preschool. If Head
Start makes a dif-
ference, we would expect to see higher reading scores for that
group as compared to
those who did not attend any preschool groups. Ideally, the
Head Start group would
have scores at least as high as those who attended nursery
schools. Using statistical
controls is a strong quasi-experimental design to employ in the
field.
We often see statistical controls used in analyzing polling data.
For example, a
national exit poll conducted by NBC was used to analyze how
young people voted in
DESIGNS FOR RESEARCH
it might be possible to track them. Unlike a controlled
laboratory experiment, participation in
Medicaid is not a constant. Some might remain on Medicaid for
years, but others will cycle off
as their earnings rise above the poverty level. Research in this
area is very difficult.
The second study, by Sommers et al. (2012), used a pre- and
postcomparison quasi-
experimental design with statistical controls. New York, Maine,
and Arizona expanded Medic-
aid eligibility in 2000. The researchers compared outcomes with
those of neighboring states

that did not expand Medicaid. They looked at data five years
before and after the expansion.
Among other things, they wanted to determine whether
Medicaid expansions were associated
with changes in mortality. Medicaid expansions were associated
with a significant reduction
in adjusted all-cause mortality. Mortality reductions were
greatest among older adults, non-
whites, and residents of poorer counties. They concluded: "State
Medicaid expansions to cover
low-income adults were significantly associated with reduced
mortality as well as improved
coverage, access to care, and self-reported health."
73
the 2008 presidential election (Keeter et al. 2008). Defining
young voters as eighteen
to twenty-nine years old and old voters as aged thirty and over,
the polltakers found
that 66 percent of all young voters reported they had voted for
Barack Obama. In
contrast. 50 percent of the older voters reported voting for
Obama.
Statistical controls allow the researchers to make even finer
slices. How did race
affect the votes of the young and the not so young? Race is now
the control variable.
The NBC poll found that 54 percent of young white voters said
they voted for Obama.
In contrast 41 percent of older white voters said they voted for
Obama.
LONGITUDINAL STUDIES

Longitudinal studies are another type of quasi-experimental
design that can be used
to measure change after a program or event. These have more
measurement points
than a simple before-and-after design. There are two approaches
for gathering the
data for longitudinal studies. The cross-sectional approach takes
a different "slice" of
the population of interest at each point in time: the result is that
different people are
used each time the data is gathered. A good example of a cross-
sectional longitudinal
study is the National Institute of Drug Abuse's annual survey of
high school seniors.
A different random sample of high school seniors is selected
every year. In 2011,
46,733 students from 400 public and private schools in the
eighth, tenth, and twelfth
grades participated in this year's survey. This longitudinal
design allows researchers
to track the self-reported use of marijuana and tobacco over
time, creating a trend
line (see Exhibit 5.1 ).
The second approach is a panel design that gathers data from
the same group of
people over time. For example, the Department of Labor's
Bureau of Labor Statistics
conducts the National Longitudinal Survey of Youth (NLSY). It
began in 1979 with
a random sample of 11 ,406 people between fourteen and
twenty-one years of age.
Follow-up interviews were conducted annually with this same
group of people through
I 994. After that, biennial interviews were conducted. In
addition to a standard set of

Predictions are also possible based on trend lines, but there are
some limitations
in driving forward by looking through the rearview window.
Changes in the larger
environment can dramatically alter the accuracy of any forecast.
A big controversy
emerged in 2012 when the number of people receiving food
stamps spiked. Look-
ing at past trends proved to be an inaccurate predictor of future
demand because of
increased unemployment and changes to eligibility rules.
An intelTupted time series design is a good option for program
evaluation when
there are multiple data points before and after a specific event
or a program or policy
is implemented. Researchers would be looking for a change in
the trend line after a
program was implemented. In the notation. it looks like this:
X
For example, when citizens of Washington state voted in 2011
to privatize liquor
sales. some believed there would be an increase in alcohol-
related fatalities. Research-
ers could use an inten·upted time-series design to track alcohol-
related fatalities be-
fore and after the law changed. However. this design does not
rule out other factors.
Sometimes it is possible to use an intelTupted times series

design with a comparison
group. This is called a multiple time series analysis. This is a
useful design when a
program is implemented in one place and not another. For
example, this design could
be used to look at the fatality rates before and after some states
rescinded the laws
requiring that motorcyclists use helmets compared to the states
that did not. The
notation would look like this:
o, 0 2 o, o+ o, o(J o7 o.~ o~ 0 10
0 1 0 2 0, 0+ O, 0 6 07 Ox 0 9 0 1, 1
X 0 11 0 12 0 11 0 1 ~ 0 15 0 16
o,, 0,2 0!1 o,~ 0" o,n
Whether to use a longitudinal design (covering just a few years)
or a time-series
analysis (covering many years) will depend on the situation.
Clearly, if researchers
need quick results, they will not choose a time series analysis
unless the data are
already available.
The key point with any data collected over time is whether the
data are measured in
exact] y the same way every time. Any change creates apples-
to-oranges comparisons;
more technically. the data are no longer reliable.
While these are strong designs. it is important to keep in mind
that they are limited
in answering a cause-and-effect or impact question unless they
are able to rule out
those pesky rival explanations. Trend lines, in particular. are

not useful in explaining
why things change. We know, for example, that obesity among
children in America
has increased over time. So far. however, researchers have been
unable to come to
agreement about the causal factors.
INTERNAL VALIDITY
Researchers talk about internal validity when operating within
the Xs and Os frame-
work. Internal validity is the shorthand reminder for considering
whether other fac-
If&; .. ···.·. R--~-
~-
76 CHAPE; :
tors may have influenced the results. Social scientists have
identified some comrr -
threats to internal validity, including history, maturation,
testing, instrumentati,:-
regression to the mean, selection, and attrition. .
History is a potential threat if a particular event took place
while the study ::_
being conducted that might impact the results. For example, the
departure of t:-:
stress-provoking manager after the stress reduction program
started is an example · ·
a history effect. Using a comparison group reduces this threat.
If it is not possible :
have a comparison group, it is important to find out what was

happening at that tir·:
that may have affected the results.
Maturation is a potential threat when it is possible for skills or
abilities to incre:: c:
because the participants got older. For example, improved study
skills among ch: -
dren might be a result of maturation rather than their
participation in a study ski:
program. Perhaps the ability to concentrate improves as children
get older. Usins _
comparison group reduces this threat.
Testing can be a potential threat in research when a test is used
to measure char.;~
before and after a program. Why? It is possible that people
might have learned h,: ..
to take the test. Using a comparison group reduces this threat
because both grou::- ·
would have learned how to take the test. If the program made a
difference, participar: ·
in the program should still have higher scores.
Instrumentation refers to any changes in what gets counted or
how it gets countc.:
This is a threat in any design that uses before-and-after
measures, because any chan;:
creates an apples-to-oranges comparison. For example, a school
implements a zer -
tolerance" for-weapons program that includes posting "no
weapon" signs, education.:.
events, and conflict resolution training for all students. The
school uses the number : ·
children who brought a weapon to school before the program
began as the baseli:-~
(pre-measure). The program runs for three years and then

measures the number ·:-
children who brought a weapon to school during the last year of
the program. If t~ ~
school changed the definition of weapon during those three
years to include me:-~
items, such as Swiss army knives and metal nail files, the
results would not be a go· ~
measure of whether the program worked. The threat would be
reduced if there c:
a similar comparison school that did not have the program but
confiscated weapo:- ·
during that same time period and made the same definitional
changes about what.::_·
considered a weapon.
"Regression to the mean" is a threat only if a program or policy
is implemente .=
because of an unusually high or low measurement. Regression
to the mean is ba-.e =
on the idea that things vary over time and tend to balance out. It
is kind of a stati,' -
cal version of ''what goes up must come down." For example,
when a crackdown ,: -
speeders is implemented because of an unusually high number
of highway fataliue ·
one year, it is possible the number of highway fatalities would
have gone down tr:
next year without the program.
One way to avoid this threat is not to intervene solely on the
basis of a sing;~
extreme high or low score. However, sometimes there is public
or political pressu:-:
to do something about a perceived crisis, so public
administrators implement apr -
gram or regulation. To minimize the regression to the mean

threat, researchers wou1 ~
want to look at data over a longer period of time and/or use
comparison data fro-,
; 5
n.
-_e
f
: l
neighboring jurisdictions to get a clearer picture of the impact
of the crackdown in
the context of the natural variation in traffic fatalities.
Selection of sites or people can be a threat. The criteria for any
selection have to
be made clear along with potential impacts on the results. For
example, if different
sites are selected. are there some differences between them that
affect the results?
Are the volunteers in the stress reduction program different
from other employees in
some particular way that affects the results? Similarly, when
only a small proportion
of people asked to participate in a survey actually do. are they
different from those
who do not? That leads to the next question: do those
differences affect the results?

Selection is also a possible threat when a program manager
chooses some people
to participate in the program but not others. What are the
criteria for selection? Are
those participants different from a typical client? More
skeptically, did the program
officials select the people most likely to succeed in order to
make the program look
successful?
In fairness to program managers, however. this is a tough
situation. From a manage-
ment perspective, selecting people who are most likely to
benefit from the program may
be viewed as the best use of taxpayers· dollars. However, from
a research perspective,
selecting the best-the cream of the crop-will not give a good
measure of program
impact. because the best people might have done just as well
without the program. For
example, selecting welfare recipients with at least a high school
education and some
work experience to participate in a training program makes it
hard to tell whether the
training program actually made a difference. It is possible that a
high percentage of
these recipients would have gotten jobs without the training
program.
Attrition is a potential threat in any design that tracks the same
people over time.
It is possible that the people who dropped out of the study were
different in some
important way. For instance, researchers want to detem1ine the
efficacy of a drug
treatment program, so they track the participants over time. The

researchers state
that 75 percent of the participants who answered a survey a year
after completing the
program were drug-free. Success? Maybe. If a hundred people
started the program
and only fifty completed it, attrition is a threat to validity. What
happened to the fifty
who did not complete the program? A 75 percent program
success rate looks like
the program had a positive impact. but it is based on only half
the initial group; the
program might not be as successful as it initially appears.
WHY VALIDITY MATTERS
On March 16. 1964. President Lyndon B. Johnson delivered a
speech announcing his
proposal for a nationwide war on poverty (Grier and Jonsson
2004 ). He told Congress
and the nation: ''Because it is right, because it is wise, and
because, for the first time
in our history, it is possible to conquer poverty, I submit, for
the consideration of the
Congress and the country, the Economic Opportunity Act of
1964." The antipoverty
program includes a wide range of programs, including Head
Start, VISTA, food
stamps, Job Corps, legal aid. and community action agencies.
Exhibit 5.2 shows the poverty data for the United States. The
trend data over time
(think time series) shows a continued drop in the percentage of
people below the

78 CHAPTER 5
Exhibit 5.2 Percentage of People Living in Poverty, United
States, 1979-2011
30%
Qj
:§ 25%
f
0
~20%
0
Qi
..c
c
015%
~
"5
0.
0
0.10%
0
~
IV
.s:::
VI 5%
0%
All

1983:
22.3%
15.2%
1993:
22.7%
15.1% 15.0%
1979 1981 1983 1985 1987 1989 1991 1993 1995 1997 1999
2001 2003 2005 2007 2009 2011
Source: Shierholz and Gould 2012. Reptinted with permission
from Economic Policy Institute.
Note: Shaded areas denote recessions.
poverty line after 1960. In I964, the poverty rate was 19 percent
and dropped to II
percent by I973. Looking at Exhibit 5.2, we see the trends from
1979 to 2011. In
2011, 15 percent of Americans lived below the poverty line, and
almost 22 percent
of those under age IS were living below the poverty line. Do
these figures mean that
President Johnson's poverty program failed? Maybe yes, maybe
no.
The libertarian Cato Institute and the conservative Heritage
Foundation agree: it is
a failure. According to the Cato Institute, the government has
spent trillions of dollars
yet poverty remains "perilously close" to what it was in 1964
and the availability of
welfare has made things worse by trapping people into a state of

dependency (Tanner
2006 ). The Heritage Foundation challenges the statistics,
saying poverty is overstated
and government rewards dependency (Rector and Johnson
2004).
The Center for Budget and Policy Priorities makes the case that
the safety net
created by various poverty programs over the past 50 years
"kept 41 million people,
including 9 million children, out of poverty in 20 12'' (Sherman
et al 20 12). The
percentage of people living in poverty is less than it was in I960
and severe hunger
is rare in America today because of the food stamp program and
other nutrition pro-
grams such as the Special Supplemental Nutrition Program for
Women, Infants and
~~c-
r
! 80
~
:;-
-~
Exhibit 5.3 Common Research Designs Using the Xs and Os
Framework
Experimental

Always uses random assignment to treatment and control
groups. The classic experimental designs
also collect data before and after treatment. However, variations
may not collect before measures. It
is the strongest design for controlling threats to internal validity
but weak in external validity. While
hard to do in the public sector, it is not impossible.
Quasi-experimental
No random assignment. Selection is a potential threat. May be
reasonably strong to answer impact
and cause-and-effect questions; generally strong in controlling
for history and regression to the
mean. May be weak on external validity.
Nonequivalent groups: Comparison of group with program to
group without the program. Controls
for history and maturation if comparison group is a close match;
selection and attrition may be
threats.
Natural experiments: Situations in which there are naturally
occurring comparison groups and
before-and-after measures.
Matched groups: Matches program and comparison groups on
key variables to control for
selection threat.
Correlational design with statistical controls (sometimes called
causal-comparative or Ex post
fact): Collects data from all or a sample of people, cases, units,
etc., and uses statistical
techniques to create comparison groups in order to compare
outcomes and control for rival
explanations.
Longitudinal

Data collected over time:The key is that the measures are
defined and data collected the same
way; attrition, testing, and instrumentation are possible threats.
Cross-sectional: Collects the same data at a few points in time
from different people.
Panel: Collects same data from the same people at various
points in time.
Time series: Collects the same data at many points in time.
Useful for describing trends but
does not explain why things change.
Interrupted time series: Data before and after the program from
different people or the same
people. May face selection and instrumentation threats.
Multiple time series: Comparison of data over time.
Nonexperimental
While useful in answering descriptive and normative questions,
it is weak for answering impact or
cause-and-effect questions.
Before and after: Collects data on key measures before and after
program; controls for history
and maturation if comparison group is a close match; selection,
regression to the mean, and
attrition may be threats.
• Static group comparison: Collects key day after the program
and compares with control group.
Selection, history, and regression to the mean may be threats.
One-shot: Provides a snapshot after a program or policy is
implemented or a picture of one
point in time. There are no before measures and no comparison.
History and selection may
be threats.

have long known about the limits of "cookie cutter" or one-size-
fits-all approaches.
Communities are different, and what works in one might not
work in another. So-
phisticated users of research results who are concerned about
external validity will
ask some questions: "Does what happens in this study reflect
what occurs in other
places where the program is also being conducted?" "How
similar or dissimilar are
those communities to ours?" and "Do their success factors exist
here?"
As good as the Oregon Health Insurance Experiment is, it has
limited external
validity. What happens in Portland might not be particularly
representative of the
rest of Oregon and perhaps even less representative of the rest
of the nation. But any
study is limited by its scope and boundaries.
When critiquing study results, it is reasonable to expect the
researchers to identify
potential threats. When possible, they should take steps to
mitigate these threats. If things
are beyond their ability to control, it is reasonable to expect the
researchers to identify
possible limitations and provide cautions about drawing
conclusion from the results.
CONCLUSION

The situation and type of research question determine which
design elements are used.
No design is perfect nor can a single design be applied to every
research question because
every situation is unique. Exhibit 5.3 summarizes the common
research designs in the
Xs and Os framework. If the researcher is asking a descriptive
question or a normative
question, then a nonexperimental design is sufficient. However,
to demonstrate that a
program hac! an impact or that a cause-and-effect relationship
exists, the design has to
be rigorous enough so that other possible explanations are ruled
out.
The strongest design for cause-and-effect questions is an
experimental design.
Random assignment is its unique feature, and this controls for
all kinds of factors
that might affect the observed results. However, quasi-
experimental designs are more
commonly used in public administration research because it is
often not possible
to randomly assign people to programs or policies. Researchers
face challenges in
conducting research in the public sector (see Application 5.3 ).
One takeaway lesson for sophisticated consumers of research
results is to look
beneath the surface whenever anyone claims to have found a
program impact or a
program failure. If it is difficult to discern a strong research
design in terms of the
Xs and Os framework, then caution is warranted in accepting
claims of causality as

truth. Three tough questions to ask are:
1. Is there something else other than the program that could
explain these
results?
2. Has something been left out of the study that might alter the
results or reflect
a bias?
3. Is the research design strong enough to support the
conclusions?
The final takeaway lesson is to remember that given all the
challenges in designing
strong impact studies and eliminating all the threats to internal
and external validity,
we often know a lot less than we think we know about cause-
and-effect relationships
and program impacts.

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