Which function would you use to test for a relationship between students attendance and their test scores quizlet?

take an equation f(x , y) = x² + y³

if you are taking the partial derivative of y with respect to x, you are measuring the rate of change in the function at a certain point (a, b)

y, however, is fixed, and will always equal b

measuring JUST the rate of change of the other portion, x, as f(x, y) increases

therefore, when taking the derivative of each part of the equation, y is treated as a

Reflexes-- An infant learns about objects by grasping them (another finger¸ a toy¸ etc.) in different ways.

Combining secondary circular reactions-- An infant removes a blanket and picks up a toy that was previously hidden by her parent.

Primary circular reactions-- An infant repeatedly puts her fingers into her mouth and sucks on them.

Tertiary circular reactions-- An infant engages as a little scientist¸ banging on different pots and pans with the same wooden spoon to hear how the sounds differ.

Secondary circular reactions-- An infant throws different toys and books onto the floor from his car seat.

Mental representation-- An infant remembers¸ and may attempt to reproduce¸ behaviors and/or words previously used by others.

The basic idea behind the identification strategy can be illustrated using the simple two‐by‐two table (Table 3),
which shows means of education and wages for different cohorts and program levels. Regions are separated in
"high program" and "low program" regions. Panel A compares the educational attainment and the wages of
individuals who had little or no exposure to the program (they were 12 to 17 in 1974) to those of individuals who
were exposed the entire time they were in primary school (they were 2 to 6 in 1974), in both types of regions. In
both cohorts, the average educational attainment and wages in regions that received fewer schools are higher than
in regions that received more schools. This reflects the program provision that more schools were to be built in
regions where enrollment rates were low. In both types of regions, average educational attainment increased over
time. However, it increased more in regions that received more schools. The difference in these differences can be
interpreted as the causal effect of the program, under the assumption that in the absence of the program, the
increase in educational attainment would not have been systematically different in low and high program regions.
The identification assumption should not be taken for granted. However, an implication of the identification
assumption can be tested because individuals aged 12 or older in 1974 were not exposed to the program. The
increase in education between cohorts in this age‐group should not differ systematically across regions. Table 3,
panel B, presents this control experiment, by considering a cohort aged 18 to 24 in 1974 and a cohort aged 12 to 17
in 1974. The estimated differences in differences are very close to 0. These results provide some suggestive
evidence that the differences in differences are not driven by inappropriate identification assumptions, although
they are imprecisely estimated. In panel B, for example, the differences in differences are insignificantly different
from 0 but also from the differences in differences in panel A.

To exploit the variation in treatment intensity across regions and cohorts, this strategy can be generalized to a
regression framework. Consider first the difference between the average education of a young cohort exposed to
the program and that of an older cohort not exposed to the program. If additional schools led to an increase in
educational attainment, the difference will be positively related to the number of schools constructed in each
region. Table 4 (columns 1‐3) presents estimates of this exercise. Panel A compares children aged 2 to 6 in 1974
with children aged 12 to 17 in 1974. In column 1, the specification controls only for the interaction of a cohort of
birth dummy and the population aged 5 to 14 in 1971. The suggested effect is that one school built per 1,000
children in‐ creased the education of the children aged 2 to 6 in 1974 by 0.12 years for the whole sample, and by
0.20 years for the sample of wage earners.
This interpretation relies on the identification assumption that there are no omitted time‐varying and region‐
specific effects correlated with the program. The allocation of schools to each region was an explicit function of the
enrollment rate in the region in 1972. Therefore, the estimate could potentially confound the effect of the program
with mean reversion that would have taken place even in its absence. The identification assumption will also be
violated if the allocation of other governmental programs initiated as a result of the oil boom (and potentially
affecting education) was correlated with the allocation of schools.
Duflo (2001) present specifications that control for the interactions between cohort dummies and the enrollment
rate in the population in 1971, as well as for interactions between cohort dummies and the allocation of the water
and sanitation program, the second largest program centrally administered at the time. Controlling for both the
enrollment rate and the water and sanitation program makes the estimates higher (columns 2 and 3), suggesting
that the estimates are not upwardly biased by mean reversion or omitted programs.
Panel B of Table 4 shows the results of the control experiment (comparing the cohort aged 12 to 17 to the cohort
aged 18 to 24 in 1974). If, before the program was started, education had increased faster in regions that received
more schools, panel B would show (spurious) positive coefficients. But the impact of the "program" is very small
and never significant. The coefficients are statistically different from the corresponding coefficients in panel A.
Although this is not definitive evidence (education level could have started converging precisely after 1973), it is
reassuring.
Even if the identification assumption is satisfied, the coefficient may slightly overestimate the effect of the program
on average education. Note that such a large program could potentially have affected the returns to education by
increasing the stock of primary school graduates. Individuals' education choices could then have responded to this
decrease in the returns to education. To the extent that Indonesia is an integrated labor market, the returns to
education would have declined in the entire country. The estimates do not take this negative effect of the program
into account because it is common to all regions. This effect, however, is not likely to be very large. Its size
ultimately depends on the elasticity of the demand for educated labor (which is likely to be low in a rapidly growing
economy), the sensitivity of educational choice to perceived returns to education, and the extent of integration in
the Indonesian labor market.

Duflo (2001) use the variation in treatment intensity across regions and cohorts, and generalizes the
strategy to a regression framework. First she considers the difference between the average education of a
young cohort exposed to the program and that of an older cohort not exposed to the program. If additional
schools led to an increase in educational attainment, the difference will be positively related to the number
of schools constructed in each region. The regression specification is as follows:
S = education of individual I born in region j in year k. T is a dummy indicating whether the individual
belongs to the "young" cohort, alfa is a district of birth fixed effect, P denotes the intensity of the program
in the region of birth and C reflects region specific effects. Using Equation (1) Duflo (2001) compares
children aged 2 to 6 in 1974 with children aged 12 to 17 in 1974, controlling only for the interaction of a
cohort of birth dummy and the population aged 5 to 14 in 1971. The suggested effect is that one school
built per 1,000 children increased the education of the children aged 2 to 6 in 1974.
This interpretation relies on the identification assumption that there are no omitted time‐ varying and
region‐specific effects correlated with the program. The allocation of schools to each region was an explicit
function of the enrollment rate in the region in 1972 (low enrolment rates = more schools build). Therefore,
the estimate could potentially confound the effect of the program with mean reversion that would have
taken place even in its absence. The identification assumption will also be violated if the allocation of other
governmental programs initiated (and potentially affecting education) was correlated with the allocation of
schools. Duflo (2001) therefore control for the interactions between cohort dummies and the enrollment
rate in the population in 1971, as well as for interactions between cohort dummies and the allocation of
the water and sanitation program (the second largest INPRES program centrally administered at the time).
Controlling for both the enrollment rate and the water and sanitation program makes the estimates higher
suggesting that the estimates are not upwardly biased by mean reversion or omitted programs. Duflo
(2001) again carries out a control experiment (comparing the cohort aged 12 to 17 to the cohort aged 18 to
24 in 1974). If, before the program was started, education had increased faster in regions that received
more schools, the control experiment would show (spurious) positive coefficients. But the impact of the
"program" in the control experiment is very small and never significant.
Even if the identification assumption is satisfied, the coefficient may slightly overestimate the effect of the
program on average education. Note that such a large program could potentially have affected the returns
to education by increasing the stock of primary school graduates. Individuals' education choices could then
have responded to this decrease in the returns to education. To the extent that Indonesia is an integrated
labor market, the returns to education would have declined in the entire country. The estimates do not
take this negative effect of the program into account because it is common to all regions. This effect,
however, is not likely to be very large. Its size ultimately depends on the elasticity of the demand for
educated labor (which is likely to be low in a rapidly growing economy), the sensitivity of educational
choice to perceived returns to education, and the extent of integration in the Indonesian labor market.

Angrist and Lavy (1999) aim to estimate the effect of class size on educational achievement (test
scores in reading and math). Since class size is not a random variable, they use the class-size
function generated by Maimonides' rule to construct instrumental variables in the estimation of the
class-size effect on test scores in Israeli public schools. Maimonides' rule says that a class should
not be larger than 40 pupils: when 41 pupils are enrolled, the class should be split in two. This rule
creates a discontinuity in the relationship between enrollment and class size at regular intervals
(enrollment multiples of 40). In that way, they can match the nonlinearity or discontinuity in the
relationship between the rule and the actual (observed) class size. This strategy was inspired by
Campbell (1969).
The graph shows the class-size function generated by the Maimonides' rule and the actual school
class sizes. At enrollment levels that are not integer multiples of 40, class size increases
approximately linearly with enrollment size. But average class size drops sharply at integer
multiples of 40. The figure shows that average class size almost never reaches 40 when the
enrollment is less than 120, even though the class-size function predicts a class size of 40 when the
enrollment is 40, 80, 120, etc. This is because schools can sometimes afford to add extra classes
before reaching the maximum class size.
The problem with Angrist and Lavy's (1999) approach could be that the test scores are affected by
some mechanism other than the class size. For example, both class size and instrument could be a
function of the size of enrollment of cohorts. Different factors correlated with the enrollment and
class size that are captured in the error term of the estimation equation are also likely to be
correlated with pupil achievement. However, Angrist and Lavy (1999) assume that any other
mechanism that can affect the test scores is likely to have a smoother effect - not discontinuous like
the instrument. To control for any other relationship between enrollment and test scores, they
include control functions of enrollment in the vector of covariates.
Angrist and Lavy's (1999) results are valid when the selective manipulation (self-selection) by
parents can be ruled out. In Israel, socioeconomic status is inversely related to local population
density. Better schools might face increased demand if parents selectively choose districts on the
12
basis of school quality. At the same time, more educated parents may try to avoid overcrowded
schools by moving to districts they assess will have smaller classes. This could cause correlation
between unobserved parental preferences for child education and the instrumental variable used to
predict the class size. The authors judge that this form of bias is small in practice. Manipulation of
class size by parents is limited by the fact that Israeli pupils must attend a neighborhood school.
Also, very few Israeli children are sent to private schools in order to tackle the problem of large
enrollment.

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