We consider the challenges and implications of controlling for school contextual bias when modeling teacher preparation program effects. Because teachers are not randomly distributed across schools, failing to account for contextual factors in achievement models could bias preparation program estimates. Including school fixed effects controls for school environment by relying on differences among student outcomes within the same schools to identify the program effects, but this specification may be unidentified. Using statewide data from Florida, we examine whether the inclusion of school fixed effects is feasible, compare the sensitivity of the estimates to assumptions underlying for fixed effects, and determine what their inclusion implies about the precision of the preparation program estimates. We discuss the implications of our results on the feasibility, precision, and ranking of programs using the school fixed effect model for policy makers designing teacher preparation program evaluation systems.

On 17 February 2009, President Obama signed into law the American Recovery and Reinvestment Act of 2009. This historic legislation included $4.35 billion for the Race to the Top Fund (RTTT), a competitive grant program designed to reward states that are demonstrating success in raising student achievement scores and developing effective teachers and principals. The selection criteria included a provision on improving the effectiveness of teacher and principal preparation programs. Specifically, it awarded points to states based on “[t]he extent to which the State has a high-quality plan and ambitious yet achievable annual targets to link student achievement and student growth data to the students’ teachers and principals, to link this information to the in-State programs where those teachers and principals were prepared for credentialing, and to publicly report the data for each credentialing program in the State” (USDOE 2009, p. 10). Following the announcement of RTTT winners, in September 2011 the Department of Education released the Obama Administration's plan for teacher education reform and improvement (USDOE 2011). This comprehensive agenda describes the disbursement of federal money in three areas: institutional reporting and state accountability, reform financing of students preparing to become teachers, and targeted support to institutions that prepare teachers from a diverse background. States will be provided funds to identify top-tier and low performing teacher preparation programs based on three outcome measures: student learning growth, job placement and retention, and customer satisfaction survey results. In highlighting the goals of the new initiative, Secretary Arne Duncan indicated in remarks at the Education Sector Forum that “[a] good feedback loop and accountability system would reward high-performing teacher preparation programs and scale them up. It would help programs in the middle of the spectrum to self-correct and improve. And it would support states to reshape low-performing programs or eliminate low-performers that fail to improve over time, even after receiving help.”1 A persistent and unresolved concern with the value-added models (VAMs) that are proposed for evaluating teacher preparation programs is the existence of contextual effects of the schools where the teachers teach.2 Because teachers from any one preparation program are hired in more than one school, the growth in student achievement associated with the preparation program will come from various sources (Boyd et al. 2009). In addition, new teachers are not randomly distributed across schools within the state. For example, there is anecdotal evidence from other states that schools tend to hire teachers from local preparation programs, suggesting there is a geographic clustering of program graduates. If, in addition to geographic preferences in hiring decisions, student ability is not evenly distributed across schools, then failing to account for school contextual factors could bias preparation program estimates. In this paper we focus on the feasibility and implications of controlling for school contextual factors when comparing teacher preparation programs.3 Policy makers may wish to remove the differences in schools when comparing teacher preparation programs using student growth measures. One method to overcome observed differences in schools is to include school characteristics in the VAM. An alternative specification of the VAMs that overcomes unobserved differences in school context includes school fixed effects. With school fixed effects, comparisons among teachers from different programs are made within schools. School fixed effects may be desirable in preparation program models because they control for unobserved factors that are potentially correlated with school quality. It is important to understand, however, whether the inclusion of school fixed effects is feasible in this setting, what the sensitivity of the estimates to underlying assumptions for fixed effects are, and what their inclusion implies about the precision of the preparation program estimates and the resulting rankings of preparation program effectiveness. When fixed effects are included in a regression, a primary concern is whether these coefficients are identified. Preparation programs not directly sharing teachers in schools can still be compared indirectly, as long as there is some linkage with teachers from other programs that teach in the same school. However, if preparation program graduates are not sufficiently mixed across schools, this type of estimation is not feasible. Identification depends on the time horizon of the data being used to estimate program effects. In the simplest case, a cross-section of recent graduates and the schools in which they end up teaching may be used, which could provide single-year estimates of program effects. This ensures that programs are being compared based on graduates teaching in the same school at the same point in time. This also limits the ties between programs, however, as many schools may not have recent graduates from multiple programs teaching there during any one school year. Alternatively, one can use a multi-year window of successive cohorts of graduates and estimate average program effects over a longer time horizon. Increasing the length of the window increases both connectivity of preparation programs and the power to discern among them, but requires time invariance of model parameters. Even when the time horizon of the data permits the inclusion of school fixed effects in the model, the extent to which the estimation relies on the indirect linkages of preparation programs needs to be considered. The inclusion of school fixed effects assumes homogeneity of effects, namely, that the teachers and schools that create ties among the preparation programs do not have different effects than other teachers or schools in the state. The larger the reliance on indirect linkages, the more sensitive are the assumptions regarding the homogeneity of effects. In addition, indirect linkages can make estimates imprecise, with the potential for significant variance inflation. To understand the implications of the homogeneity assumption we use tools from social network analysis to identify the key teachers and schools creating direct links in our preparation program/school network and we consider whether these teachers and schools are representative of teachers and schools throughout the state. Another consideration for evaluating preparation program effectiveness is the sample of teachers to include in the analysis. In order to separate the effect of the preparation program from other factors, it may be desirable to restrict the sample to recent graduates of the preparation program. Including school fixed effects with only inexperienced teachers can greatly reduce the sample used to estimate the program effects, however, which can result in variance inflation of program effects. Although including experienced teachers in the modeling can help make the analysis feasible and may be more desirable from a policy perspective, this specification may falsely imply that the preparation program effect is constant for all levels of teacher experience. This paper uses a case study of elementary school teachers and their preparation programs from the state of Florida in 2000–04 to explore the feasibility, underlying assumptions, variance inflation, and sampling choice implications of controlling for school context in the estimation of preparation program effects. We examine whether the school fixed effect parameters are identified and the difference in the precision of the program estimates under different modeling choices. We also consider whether program estimates with school fixed effects are biased due to violations of the assumptions underlying the fixed effect specification and the implications of restricting the teacher sample to inexperienced teachers. We then estimate three specifications of student achievement growth models: no school controls, school covariates (such as percent black and percent free lunch), and school fixed effects. Using the estimated program effects, we rank the preparation programs in order of effectiveness, and examine the sensitivity of the rankings to the modeling choices. Our findings indicate that although there is some regional clustering of program graduates, new teachers from many programs are hired by schools across the state of Florida. Therefore, school fixed effects can be included in the student achievement model as long as three or more years of data are used in the estimation. However, we find evidence that schools and teachers integral to connecting preparation programs are different from the average within the state, with disproportionately larger Hispanic and immigrant populations in schools and more Hispanic teachers. These differences in the schools and teachers that identify the estimates challenge the plausibility of the homogeneity assumption required by the fixed effects estimation. Importantly for policy makers, we find that the rankings of preparation programs’ effectiveness are sensitive to the inclusion of school fixed effects. When comparing the ranking quartiles of preparation programs with and without school fixed effects, we find significant changes to the programs that are ranked in the top and bottom quartiles under different specifications. For example, regardless of our sample restrictions, we find at least one preparation program that is ranked in the bottom quartile of rankings without school fixed effects and the top quartile of rankings with school fixed effects. The quartile rankings of preparation programs are more stable across the specifications for low performing programs as compared to top-tier programs. Finally, we find that including school fixed effects results in less precise preparation program estimates. Even with a five-year window there is significant variance inflation due to the inclusion of school fixed effects. The variance inflation grows rapidly as we shorten the window for estimation to one or two years, primarily because many more graduates teach in schools with graduates from a single program and thus do not contribute to program estimates in models with school fixed effects. Including experienced teachers in the estimation sample has an effect on the variance inflation for some preparation programs. Based on these results, we argue that states will need to choose among three options for modeling preparation program effectiveness, each with its own drawbacks. The first option is to estimate models without school fixed effects and make conclusions about preparation programs that may be sensitive to the model's untestable assumption of no school contextual effects. Alternatively, if school covariate data are available, states should consider an approach that controls for observable school characteristics. This may mitigate bias from nonrandom assignment of program graduates to schools but does not account for unmeasured school conditions that can impact job placements and estimates of the productivity of program graduates. Finally, states could choose to estimate models with school fixed effects that take into account both measured and unobserved time-invariant school characteristics. This may require relying on a small and atypical set of schools and teachers to identify the models which yield much less precise estimates. It is unclear which of these three approaches will yield estimates with the smallest mean square errors and the least bias. States may need to describe the uncertainty of the model they use but this could weaken the utility of estimates. Without clear evidence for or against contextual effects and the sensitivity of conclusions about programs like we found in Florida, states may need to reconsider if this approach alone can provide useful information about preparation programs. The remainder of the paper is organized as follows. First, we review previous studies that have compared teacher preparation programs on the basis of the outcomes of the public elementary and secondary students taught by their graduates. Second, we present the VAM and the exploration of the data regarding the feasibility and suitability of the school fixed effect estimation. Next, we present the preparation program effectiveness estimates under alternative model specifications and, finally, we conclude with a summary and discussion of our findings. Due in large measure to extensive data requirements, there are only a handful of existing studies that have attempted to link value-added measures of teacher performance to the preparation programs from which the teachers graduated. These include studies of teachers in seven states: New York, Florida, Louisiana, Kentucky, Texas, Missouri, and Washington. These studies have dealt with the problem of school contextual effects in different ways. In their study of New York City public school teachers, Boyd et al. (2009) include school fixed effects in their model. They do not discuss the implications of this choice in terms of the overlap of program graduates in schools or the impact of school fixed effects on the precision of their estimated program effects. They find considerable variation in teacher value-added across preparation programs but do not provide standard errors of these effects. Sass (2008) and Kukla-Acevedo, Streams, and Toma (2009) also include school fixed effects in the achievement models they use to estimate preparation program effects in Florida and Kentucky, respectively. Sass estimates models with and without school fixed effects and finds that the magnitude and significance of estimated program effects are very sensitive to this choice. Although specific estimates are quite variable, in general the effect sizes of programs tend to be larger in absolute value and standard errors smaller when school effects are not included in the model. This suggests that either differences exist among program graduates teaching in different schools or that school indicators are correlated with program indicators, and including school effects increases the variance of estimates. The work of Kukla-Acevedo, Streams, and Toma (2009) illustrates many of the practical difficulties in conducting a value-added based assessment of teacher preparation programs. Because of data limitations, their analysis focuses on three preparation programs (A, B, and C), and eleventh grade math teachers in just three of Kentucky's 125 school districts. In one district, two-thirds of eleventh grade math teachers were graduates of institution A, and none had received a degree from institution C. In the second district, a plurality of teachers came from institution C and none from A, whereas the third district hires most of its teachers from institution B, and none from A. This extreme geographic clustering of teachers means there is little chance that teachers from some program pairs will be teaching in the same schools and great potential for contextual effects bias to exist. The lack of overlap among graduates also increases the variance inflation due to the inclusion of school effects. Perhaps as a result, the authors found no significant program effects. Noell and co-authors, in their studies of teacher preparation program effects in Louisiana (Noell et al. 2009; Gansle et al. 2010) take a different course when faced with the possibility of regional separation of graduates from different preparation programs. These authors exclude school fixed effects and include school-level aggregate student demographics and prior achievement in the models instead. They find few significant differences among programs. If these aggregates proxy for all the school contextual effects, then they have found an efficient way to remove potential bias from contextual effects; otherwise, their estimates may be biased. Mellor et al. (2010), in their study of University of Texas teacher training programs, also excluded school fixed effects from the models and included a school effectiveness measure (based on school-wide test performance growth) and district indicators instead of school fixed effects because of limited overlap of program graduates in schools. Koedel et al. (2012) examine teacher preparation programs in Missouri, and present results for models with school fixed effects, school covariates, and without school fixed effects. Across model specifications they consistently find small to no differences in teacher preparation program effectiveness. They note that existing studies overstate the significance of teacher training effects by not appropriately accounting for the clustering of teachers within program. Finally, Goldhaber and Liddle (2012) use district and school covariates and fixed effects to examine the impact of teacher preparation programs in Washington state on the effectiveness of teachers trained within the state. Compared with out-of-state trained teachers, the effectiveness of within-state programs is relatively stable across the model specifications. Clearly, controlling for school contextual effects is a concern when using VAMs to assess teacher training programs. Understanding the implications of including controls for school contexts will be useful in future attempts at such modeling, such as those to be conducted by the Race to the Top winners. Eleven states and the District of Columbia were announced as winners of RTTT funds on 24 August 2010. As one of the winners of the competition, the state of Florida will receive$700 million, impacting over 2.6 million students and over 180,000 teachers in 4,250 schools.4 To meet the requirements of RTTT, Florida will be linking student achievement growth to the preparation program where the students’ teachers were trained for the purpose of evaluating these programs.5

Additionally, with rich administrative data on teachers and student outcomes and information about school and preparation programs for teachers, Florida is well suited for this study. Data for our analysis come from three sources. The Florida Education Data Warehouse (FL-EDW) provides longitudinal data on all public school teachers, including demographic information, experience, educational attainment, and certification status. Each classroom has a unique identifier, so we can reliably link teachers and students to specific classrooms at each grade level.

The determination of whether a teacher obtained initial certification by graduating from a teacher preparation program or by an alternative route, and the institution of preparation program completers, is accomplished by linking data files from the Florida Department of Education's Office of Teacher Certification with the FL-EDW data. The addresses of schools come from the Florida Department of Education's Master School ID file. Preparation institution addresses come from the Web sites of the individual colleges and universities. These address data are then geocoded with latitudes and longitudes for mapping teacher preparation institutions and the schools in which preparation program graduates teach.

Until recently, the state administered two sets of reading and math tests to all third through tenth graders in Florida. The Sunshine State Standards Florida Comprehensive Achievement Test (FCAT-SSS) is a criterion-based exam designed to test for the skills that students are expected to master at each grade level. It is a high-stakes test used to determine school grades and student retention in some grades. The second test is the FCAT Norm-Referenced Test (FCAT-NRT), a version of the Stanford Achievement Test used throughout the country. No accountability measures are tied to student performance on the NRT.

The focus of our analysis is on elementary schools and elementary preparation programs. We define an elementary school preparation program as one with a graduate teaching in self-contained regular education classrooms in grades 4 or 5 in a Florida public school during our study period (2000–04). Elementary education is by far the largest program offered by the training programs. Preparation programs offer varying mixes of programs of study and within an institution, the training of teachers can vary among them. Further, as Sass (2008) shows, the pre-college ability of future teachers differs significantly across certification areas within an institution.

Due to both population growth and a constitutionally mandated class-size restriction, Florida was a net importer of teachers during our period of study (2000/01–2004/05). In addition to significant numbers of teachers trained in other states, Florida had alternative certification programs in place that served as pathways into teaching for many teachers. In fact, less than half of newly certified elementary education teachers in Florida obtained their certification as a result of graduating from an approved Florida preparation program.6 Among teachers obtaining certification by completing a Florida preparation program, about three-fourths were graduates of public universities and the remainder graduated from private universities or four-year public colleges (Yecke 2006). Out-of-state and alternatively certified teachers are included in the value-added analysis of teacher quality, but we only present comparisons between the average performance of teachers from different Florida preparation programs.7

There are thirty-three preparation programs with at least one graduate teaching fourth- or fifth-grade mathematics or English language arts in a Florida public school during the 2000–01 to 2004–05 school years.8 To be included in the analysis, a teacher must be teaching in an elementary school in grades 4 and 5 at some point during our five-year data window.9 For some analyses we restrict the sample to teachers who have two or fewer years of experience (i.e., in their first, second, or third year of teaching). As shown in table 1, the majority of the elementary school teachers are teachers with more than two years of experience. Inexperienced teachers who were certified out of state or through alternative pathways in Florida make up a large percentage of the remaining teachers. Finally, for inexperienced teachers certified in Florida, the preparation programs range in number of employed elementary mathematics or English language arts teachers (in grades 4 and 5) from 496 all the way down to just one graduate during the five-year window.

Table 1.
Number of Teachers by Experience and Certification Status
Program IDNumber of Teachers
Experienced Teachers 6,688
Inexperienced, Alternative Cert. 1,594
Inexperienced, Out of State Cert. 1,231
Inexperienced, Cert. in Prep Program 25 496
Inexperienced, Cert. in Prep Program 1 304
Inexperienced, Cert. in Prep Program 5 293
Inexperienced, Cert. in Prep Program 2 286
Inexperienced, Cert. in Prep Program 4 279
Inexperienced, Cert. in Prep Program 8 201
Inexperienced, Cert. in Prep Program 7 174
Inexperienced, Cert. in Prep Program 3 163
Inexperienced, Cert. in Prep Program 10 148
Inexperienced, Cert. in Prep Program 6 140
Inexperienced, Cert. in Prep Program 9 124
Inexperienced, Cert. in Prep Program 11 104
Inexperienced, Cert. in Prep Program 14 50
Inexperienced, Cert. in Prep Program 13 45
Inexperienced, Cert. in Prep Program 12 43
Inexperienced, Cert. in Prep Program 16 41
Inexperienced, Cert. in Prep Program 15 28
Inexperienced, Cert. in Prep Program 21 28
Inexperienced, Cert. in Prep Program 18 24
Inexperienced, Cert. in Prep Program 22 23
Inexperienced, Cert. in Prep Program 23 22
Inexperienced, Cert. in Prep Program 24 22
Inexperienced, Cert. in Prep Program 20 17
Inexperienced, Cert. in Prep Program 19 16
Inexperienced, Cert. in Prep Program 17 15
Inexperienced, Cert. in Prep Program 28 13
Inexperienced, Cert. in Prep Program 27 12
Inexperienced, Cert. in Prep Program 26 11
Inexperienced, Cert. in Prep Program 29
Inexperienced, Cert. in Prep Program 33
Inexperienced, Cert. in Prep Program 30
Inexperienced, Cert. in Prep Program 32
Inexperienced, Cert. in Prep Program 31
Program IDNumber of Teachers
Experienced Teachers 6,688
Inexperienced, Alternative Cert. 1,594
Inexperienced, Out of State Cert. 1,231
Inexperienced, Cert. in Prep Program 25 496
Inexperienced, Cert. in Prep Program 1 304
Inexperienced, Cert. in Prep Program 5 293
Inexperienced, Cert. in Prep Program 2 286
Inexperienced, Cert. in Prep Program 4 279
Inexperienced, Cert. in Prep Program 8 201
Inexperienced, Cert. in Prep Program 7 174
Inexperienced, Cert. in Prep Program 3 163
Inexperienced, Cert. in Prep Program 10 148
Inexperienced, Cert. in Prep Program 6 140
Inexperienced, Cert. in Prep Program 9 124
Inexperienced, Cert. in Prep Program 11 104
Inexperienced, Cert. in Prep Program 14 50
Inexperienced, Cert. in Prep Program 13 45
Inexperienced, Cert. in Prep Program 12 43
Inexperienced, Cert. in Prep Program 16 41
Inexperienced, Cert. in Prep Program 15 28
Inexperienced, Cert. in Prep Program 21 28
Inexperienced, Cert. in Prep Program 18 24
Inexperienced, Cert. in Prep Program 22 23
Inexperienced, Cert. in Prep Program 23 22
Inexperienced, Cert. in Prep Program 24 22
Inexperienced, Cert. in Prep Program 20 17
Inexperienced, Cert. in Prep Program 19 16
Inexperienced, Cert. in Prep Program 17 15
Inexperienced, Cert. in Prep Program 28 13
Inexperienced, Cert. in Prep Program 27 12
Inexperienced, Cert. in Prep Program 26 11
Inexperienced, Cert. in Prep Program 29
Inexperienced, Cert. in Prep Program 33
Inexperienced, Cert. in Prep Program 30
Inexperienced, Cert. in Prep Program 32
Inexperienced, Cert. in Prep Program 31

Notes: Inexperienced teachers defined as having less than two years of experience. Program identities masked.

In addition to information on the graduates and the schools where they are working, the data include summary statistics on schools, such as student gender and racial ethnic distribution, achievement levels, average test scores and gains in achievement, student mobility measures, disciplinary incidents, grade repeaters, free or reduced price lunch status, limited English proficiency status (LEP), immigrant status, home language, parents’ language, special education status, and enrollment. The data also include characteristics of the preparation program graduates including gender, race/ethnicity, Scholastic Aptitude Test (SAT) scores (for teachers who began their college career at a four-year public university in Florida), whether they passed each of the general-knowledge licensure exams on the first try, and their score the last time they took the exam.

The explanatory variables used in our analysis are summarized in table 2. Over a quarter of the students in the sample are black, and one quarter are Hispanic. Similarly, one quarter of students and parents of students do not speak English at home. Over 50 percent of students receive free or reduced-price lunches. Almost one-third of teachers constitute our sample of inexperienced teachers because they have fewer than two years of experience.10

Table 2.
Summary Statistics of Explanatory Variables
VariableMeanStd. Dev.N
Panel (A) – Student and Teacher Characteristics
Female 0.5022 0.5000 371,624
Black 0.2457 0.4305 371,621
Hispanic 0.2489 0.4324 371,621
Asian 0.0181 0.1333 371,621
Change School 0.1403 0.3473 371,638
Student No English @ Home 0.2427 0.4287 371,624
Parent No English @ Home 0.2588 0.4380 371,604
Free Lunch 0.4491 0.4974 371,638
Reduced Lunch 0.1038 0.3059 371,638
LEP 0.0642 0.2452 371,638
Lag # Days in School 95.84 4.05 371,638
Lag # Days Suspended 0.1627 1.2200 371,638
Teacher Experience 1–2 Yrs 0.3052 0.4605 371,638
Teacher Experience 6–12 Yrs 0.2011 0.4009 371,638
Teacher Experience 13–20 Yrs 0.0833 0.2764 371,638
Teacher Experience 21–27 Yrs 0.0326 0.1776 371,638
Teacher Experience 28+ Yrs 0.0169 0.1288 371,638
Panel (B) – School Characteristics
Proportion Free Lunch 0.5674 0.2608 371,638
Proportion Black 0.2416 0.2416 371,638
Proportion Hispanic 0.2630 0.2694 371,638
Proportion Special Ed 0.1579 0.0574 371,638
Proportion LEP 0.1347 0.1418 371,638
Proportion Change School 0.1502 0.0959 371,638
VariableMeanStd. Dev.N
Panel (A) – Student and Teacher Characteristics
Female 0.5022 0.5000 371,624
Black 0.2457 0.4305 371,621
Hispanic 0.2489 0.4324 371,621
Asian 0.0181 0.1333 371,621
Change School 0.1403 0.3473 371,638
Student No English @ Home 0.2427 0.4287 371,624
Parent No English @ Home 0.2588 0.4380 371,604
Free Lunch 0.4491 0.4974 371,638
Reduced Lunch 0.1038 0.3059 371,638
LEP 0.0642 0.2452 371,638
Lag # Days in School 95.84 4.05 371,638
Lag # Days Suspended 0.1627 1.2200 371,638
Teacher Experience 1–2 Yrs 0.3052 0.4605 371,638
Teacher Experience 6–12 Yrs 0.2011 0.4009 371,638
Teacher Experience 13–20 Yrs 0.0833 0.2764 371,638
Teacher Experience 21–27 Yrs 0.0326 0.1776 371,638
Teacher Experience 28+ Yrs 0.0169 0.1288 371,638
Panel (B) – School Characteristics
Proportion Free Lunch 0.5674 0.2608 371,638
Proportion Black 0.2416 0.2416 371,638
Proportion Hispanic 0.2630 0.2694 371,638
Proportion Special Ed 0.1579 0.0574 371,638
Proportion LEP 0.1347 0.1418 371,638
Proportion Change School 0.1502 0.0959 371,638
Our value-added framework relates achievement for student i in year t(Yit) to time varying student demographic characteristics (Xit), prior year student achievement scores (Yi,t−1), experience indicators for teacher k in year t(Zkt), grade and year indicators and , respectively), and preparation program fixed effects , as expressed in equation 1:
1
One option to control for school contextual factors is to include observable school characteristics Ss, as shown in equation 2:
2
Alternatively, school fixed effects can be included in the model to capture unobserved school characteristics:
3
We compare the preparation program coefficients and precision of the estimates across the three models. In some specifications we restrict the sample to only inexperienced teachers. This restriction has implications for the identification of the school fixed effects (as discussed subsequently) as well as the size of the analysis sample. In all specifications we estimate preparation program effects for the recent graduates relative to the average Florida preparation program.11

To identify school fixed effects in the model requires all the preparation programs to be connected to the network through at least one graduate teaching in a school with graduates of other programs. Estimation of program effects controlling for school effects cannot occur if programs can be partitioned into distinct groups or strata such that programs in any one stratum are not connected to programs in any of the other strata.12 A feature of the preparation program/school network that will allow us to compare preparation programs with school fixed effects is that all of the preparation programs are connected in a single stratum.

### Regional Clustering of Program Graduates

One feature of teacher hiring decisions that could result in stratification is the regional clustering of graduates. To examine the evidence for this phenomenon in Florida, first we mapped the location of the preparation programs and schools with connections showing programs that sent graduates to a particular school. Figure 1 depicts programs and schools in Florida, where lines indicate that a new teacher was hired from a preparation program to a particular school. The shade of the line connecting schools and programs represents the strength of this connection, with darker lines indicating that more teachers were hired from the preparation program at the school. It is evident in figure 1 that although the stronger connections are regional, there are many teachers who end up teaching far away from their preparation program.

Figure 1.

Preparation Program and School Connections

Figure 1.

Preparation Program and School Connections

Close modal

Next, we verified the tendency for stronger regional connections by modeling the number of teachers from a particular program teaching in a school with at least one recent graduate from any of the programs as a function of the distance from the preparation program to the school using a generalized additive Poisson regression with a smooth function for distance. Figure 2 shows the estimated probability of one or more graduates teaching in a school as a function of distance from the preparation program. The clearly negative relationship is statistically significant, indicating that, indeed, graduates are more likely to teach in schools closer to where they graduated. This is consistent with evidence reported by other researchers working on this issue in other states (Boyd et al. 2009).

Figure 2.

Estimated Probability of Preparation Program Graduate Teaching at School with at Least One Graduate from Any Program as a Function of Distance from Program to School

Figure 2.

Estimated Probability of Preparation Program Graduate Teaching at School with at Least One Graduate from Any Program as a Function of Distance from Program to School

Close modal

### Connectivity of Preparation Programs

Using social network visualization, we are able to show that school fixed effects estimation is feasible in Florida using a five-year window. Figure 3 depicts the preparation program network for elementary schools, where a connection between two programs is defined to exist if the graduates of the program teach at the same school. All preparation programs have at least one graduate teaching in an elementary school with a graduate of at least one other program. Moreover, the ties among programs are sufficient for all programs to be connected with all other programs at least indirectly when using a five-year window.

Figure 3.

Elementary Preparation Program Network

Figure 3.

Elementary Preparation Program Network

Close modal

Next, we consider how the number of years of student achievement data used to estimate program effects influence our ability to identify school fixed effects. Our data have teachers and school links for a five-year window. If we use all five years of data, two programs will have a link through a school if both have a graduate teaching in the school sometime during the five-year window. They do not need to be teaching in the school during the same year, just during the same window. Clearly, as we lengthen the window, more programs will have links. However, lengthening the window requires the assumption that both school and program effects are constant over the entire window. A longer window increases the potential for this assumption to be violated, as school-level factors such as school leadership, instructional resources, and community support can change during the window, possibly changing the school effect. Hence, shorter windows are desirable because they require less stringent assumptions but they could break links and network connectivity, making estimates less stable, or even infeasible.

We examined the stratification in the Florida preparation program network as the window size creating links is reduced from five years to one year.13 With just a three-year window, the network of preparation programs remains fully connected, even with the regional clustering and some very small programs included in the sample. Restricting the sample to a two-year window, however, with just the 2003–04 and 2004–05 school years, results in two very small preparation programs having no graduates working in Florida elementary schools. Also, when we restrict to just these two school years, the network of programs with graduates teaching in schools is no longer fully connected because one very small program is disconnected from all other programs. The disconnected program has a single graduate working in a school with no other recent graduates during the 2004–05 school year.

The calculations for the connectivity of the preparation program network presented here were based on the sample of inexperienced teachers trained in Florida. Alternatively, we could include experienced teachers and allow for a common school effect for all teachers in Florida. Because this new sample would include more teachers, the resulting preparation program network would be more connected. Therefore, the results for inexperienced teachers represent a “lower bound” on the connectivity of the teacher preparation program network that could be achieved if assuming common school effects for experience and inexperienced teachers was justified.

### Schools in the Preparation Program Network

Although all preparation programs are connected with a five-year window, as shown in figure 1, graduates from different programs often do not teach in the same schools. This is reflected in figure 3. Many programs do not connect directly with other programs but they are connected indirectly. For instance, graduates from Program 32 teach in schools with graduates from only two other programs (Program 1 and Program 18), but these programs then connect to the rest of the network.

Indirect connections are fostered by schools that hire many recent graduates from multiple programs. For example, a few schools have graduates from five or even six programs. Such schools create links for five or six programs which can then link back to other programs, creating the connected network. As shown in table 3, schools with graduates from many preparation programs tend to be large schools, with relatively large proportions of black and Hispanic students who are English language learners with parents who do not speak English. The students in these schools also tend to be somewhat more likely to be eligible for free school meals.

Table 3.
Testing Homogeneity of School Characteristics for Schools by Number of Preparation Program Connections
School Characteristic1 Prep2 Prep3 Prep4 to 6 PrepDifference
School Size 712.23 741.71 855.22 878.47 164.85*
(266.68) (271.35) (300.51) (343.50)
Female 0.4782 0.4792 0.4825 0.4806 0.0024
(0.0416) (0.0350) (0.0218) (0.0181)
Black 0.2646 0.3089 0.2982 0.3813 0.1140*
(0.2496) (0.2875) (0.2991) (0.3180)
Hispanic 0.1695 0.2337 0.3429 0.3144 0.1472*
(0.1990) (0.2532) (0.3003) (0.3104)
Parent No English @ Home 0.1728 0.2411 0.3446 0.3448 0.1682*
(0.2022) (0.2447) (0.2804) (0.3003)
LEP 0.0882 0.1231 0.1627 0.1689 0.0817*
(0.1143) (0.1389) (0.1461) (0.1545)
Free or Reduced Lunch 0.5496 0.6306 0.6533 0.7054 0.1557*
(119.13) (104.85) (112.47) (98.87)
Math Gain Score 155.84 163.88 160.61 166.12 9.65*
(57.49) (45.38) (34.86) (37.65)
657 348 159 69
School Characteristic1 Prep2 Prep3 Prep4 to 6 PrepDifference
School Size 712.23 741.71 855.22 878.47 164.85*
(266.68) (271.35) (300.51) (343.50)
Female 0.4782 0.4792 0.4825 0.4806 0.0024
(0.0416) (0.0350) (0.0218) (0.0181)
Black 0.2646 0.3089 0.2982 0.3813 0.1140*
(0.2496) (0.2875) (0.2991) (0.3180)
Hispanic 0.1695 0.2337 0.3429 0.3144 0.1472*
(0.1990) (0.2532) (0.3003) (0.3104)
Parent No English @ Home 0.1728 0.2411 0.3446 0.3448 0.1682*
(0.2022) (0.2447) (0.2804) (0.3003)
LEP 0.0882 0.1231 0.1627 0.1689 0.0817*
(0.1143) (0.1389) (0.1461) (0.1545)
Free or Reduced Lunch 0.5496 0.6306 0.6533 0.7054 0.1557*
(119.13) (104.85) (112.47) (98.87)
Math Gain Score 155.84 163.88 160.61 166.12 9.65*
(57.49) (45.38) (34.86) (37.65)
657 348 159 69

Notes: Standard deviations in parentheses. “Difference” is taken between “1 Prep” and “4 to 6 Prep” values.

*Statistically significant at the 5 % level.

Some schools with fewer new hires can also be central to the connectivity of the network if they support connections that do not otherwise exist and link programs that then have many indirect links. The data from students in these schools may be necessary for identifying many of the program effects in our models, and consequently, these schools may have undue influence on the estimates of program effects (Belsley, Kuh, and Welsch 1980). However, because these schools can be difficult to identify, we use the betweenness centrality index, a tool from social network analysis, to identify pivotal schools within the network.14

If central schools are unusual in some ways, then their teachers may also be unrepresentative of typical program graduates, potentially resulting in bias. Schools that rank high on the betweenness centrality index (i.e., above 90th percentile of all schools on this index) are often in urban centers around the state, but they are distributed across much of the state. As shown in table 4, like schools with graduates from many different programs, highly central schools tend be large and serve high percentages of Hispanic, immigrant, and LEP students. The proportion of program graduates teaching in these highly central schools varies from zero to 100 percent in one very small school. Overall, less than a quarter of graduates from 70 percent of programs teach in these central schools.

Table 4.
Testing Homogeneity of School Characteristics for Central and Non-Central Schools
Teacher CharacteristicNon-CentralCentralDifference
School Size 738.54 835.50 96.96*
(279.02) (299.58)
Female 0.4788 0.4821 0.0033
(0.0382) (0.0192)
Black 0.2890 0.2782 −0.0108
(0.2739) (0.2643)
Hispanic 0.2125 0.2684 0.0560*
(0.2419) (0.2649)
Parent No English @ Home 0.2215 0.2731 0.0516*
(0.2381) (0.2520)
LEP 0.1080 0.1487 0.0406*
(0.1289) (0.1491)
Free or Red. Lunch 0.5922 0.6160 0.0238
(0.2523) (0.2418)
Math Gain Score 159.37 159.14 −0.23
(52.46) (32.72)
1,109 124 1,233
Teacher CharacteristicNon-CentralCentralDifference
School Size 738.54 835.50 96.96*
(279.02) (299.58)
Female 0.4788 0.4821 0.0033
(0.0382) (0.0192)
Black 0.2890 0.2782 −0.0108
(0.2739) (0.2643)
Hispanic 0.2125 0.2684 0.0560*
(0.2419) (0.2649)
Parent No English @ Home 0.2215 0.2731 0.0516*
(0.2381) (0.2520)
LEP 0.1080 0.1487 0.0406*
(0.1289) (0.1491)
Free or Red. Lunch 0.5922 0.6160 0.0238
(0.2523) (0.2418)
Math Gain Score 159.37 159.14 −0.23
(52.46) (32.72)
1,109 124 1,233

Notes: Standard deviations in parentheses. Central schools are in the 90th percentile of betweenness centrality.

*Statistically significant at the 5% level.

Given that the schools central to identification are distinctly different from other schools and have relatively few graduates from most programs, there is a significant risk that modeling with school fixed effects could actually introduce bias rather than remove it. For instance, if program graduates who are drawn to teach in large, highly Hispanic schools are different from other program graduates, then fixed effects could create biased contrasts among the preparation programs within the central schools, and the bias could ripple through all of the estimates via the indirect connections shown in figure 3.

Table 3 also shows the majority of schools hired teachers from only a single preparation program. These schools tend to be smaller and serve smaller percentages of minority (black and Hispanic), LEP, and free or reduced-price lunch–eligible students as compared with schools with multiple program graduates. The schools with graduates from a single program also tend to serve smaller percentages of students whose parents do not speak English and make smaller gains in math achievement.

The differences between schools with graduates from a single program and those with graduates from multiple programs present challenges for estimating program effects. If the context of the schools with graduates from one program is not removed by the covariates in Model 1 then the context could confound our estimates of program effects. Modeling with school fixed effects will eliminate the outcomes of students whose teachers are from a single program in the estimation of preparation program effects. This could be problematic. If teachers drawn to these schools are different from others in their programs or if programs have different effects on these teachers, then our program effects could be biased. Model 2 is the natural choice, but we must capture all the contextual variables—and we can never be certain we have.

### Plausibility of Homogeneity Assumption

Implementing school fixed effects in the preparation program VAMs requires a homogeneity of effects assumption. That is, the analysis assumes no systematic differences among teachers and schools that create the connections among programs. If program effects differ for teachers that connect programs and those that do not, then fixed effects will yield biased estimates of the program effects. Similarly, if the teachers or schools that connect programs are systematically different from other teachers or schools then differences among programs will be confounded. For instance, if only the best graduates of program A teach in schools that connect program A to program B, then the estimate of the relative effects of program A and B will be biased in favor of program A. If many graduates connect programs, this sort of selection is less likely than if few graduates support the connection, as these rare cases can be more extreme than the majority of the sample.

Table 5 shows the average characteristics of program graduates by the number of program graduates in the schools where they teach. Graduates who teach in schools with graduates from multiple programs are more likely to be minorities when compared with other graduates from their programs. They also tend to score lower on the mathematics certification exam than other graduates from their programs and have somewhat lower SAT scores. Our models do not control for these teacher attributes. To the extent that these attributes affect student achievement they will result in a correlation between the error term and the school indicators in Model 3 and thus bias the program effect estimates. Expanding our models to include these attributes could remove bias due to the observables, but given the differences in teachers on observables, we have remaining concerns that unobservable differences also exist among the teachers choosing to teach in schools that are the backbone of the fixed-effects analysis.

Table 5.
Testing Homogeneity of Teacher Characteristics by Number of Preparation Program Connections
Teacher Characteristic1 Prep2 Prep3 Prep4 to 6 PrepDifference
Male 0.1223 0.1179 0.0997 0.1250 0.0027
(0.3278) (0.3226) (0.2998) (0.3311)
White 0.8002 0.6626 0.5396 0.4814 −0.3188*
(0.4000) (0.4731) (0.4988) (0.5003)
Black 0.0994 0.1636 0.1584 0.2394 −0.1400*
(0.2994) (0.3701) (0.3653) (0.4273)
Hispanic 0.0845 0.1636 0.2859 0.2660 0.1815*
(0.2783) (0.3701) (0.4522) (0.4424)
First Pass Math 0.6415 0.5733 0.5320 0.5248 −0.1167*
(0.4800) (0.4950) (0.4996) (0.5006)
First Pass Reading 0.8074 0.7440 0.7252 0.7225 −0.0849*
(0.3947) (0.4368) (0.4470) (0.4489)
First Pass Essay 0.9358 0.9007 0.8930 0.8691 −0.0667*
(0.2453) (0.2993) (0.3096) (0.3382)
Math Test 306.04 301.75 297.57 300.05 −5.98*
(26.91) (26.62) (24.79) (25.61)
Reading Test 315.60 308.85 309.17 309.61 −5.99*
(25.59) (25.40) (24.93) (27.76)
Essay Test 7.57 7.26 7.33 7.13 0.44*
(1.60) (1.59) (1.60) (1.68)
SAT 954.27 926.67 916.27 910.22 −44.04*
(146.71) (156.71) (156.76) (154.87)
1,006 984 682 376
Teacher Characteristic1 Prep2 Prep3 Prep4 to 6 PrepDifference
Male 0.1223 0.1179 0.0997 0.1250 0.0027
(0.3278) (0.3226) (0.2998) (0.3311)
White 0.8002 0.6626 0.5396 0.4814 −0.3188*
(0.4000) (0.4731) (0.4988) (0.5003)
Black 0.0994 0.1636 0.1584 0.2394 −0.1400*
(0.2994) (0.3701) (0.3653) (0.4273)
Hispanic 0.0845 0.1636 0.2859 0.2660 0.1815*
(0.2783) (0.3701) (0.4522) (0.4424)
First Pass Math 0.6415 0.5733 0.5320 0.5248 −0.1167*
(0.4800) (0.4950) (0.4996) (0.5006)
First Pass Reading 0.8074 0.7440 0.7252 0.7225 −0.0849*
(0.3947) (0.4368) (0.4470) (0.4489)
First Pass Essay 0.9358 0.9007 0.8930 0.8691 −0.0667*
(0.2453) (0.2993) (0.3096) (0.3382)
Math Test 306.04 301.75 297.57 300.05 −5.98*
(26.91) (26.62) (24.79) (25.61)
Reading Test 315.60 308.85 309.17 309.61 −5.99*
(25.59) (25.40) (24.93) (27.76)
Essay Test 7.57 7.26 7.33 7.13 0.44*
(1.60) (1.59) (1.60) (1.68)
SAT 954.27 926.67 916.27 910.22 −44.04*
(146.71) (156.71) (156.76) (154.87)
1,006 984 682 376

Notes: Standard deviations in parentheses. “Difference” is taken between “1 Prep” and “4 to 6 Prep” values.

*Statistically significant at the 5% level.

Homogeneity could also be violated if a school tended to hire similar quality teachers regardless of the preparation program quality. For example, schools with many resources and serving highly affluent students may be able to attract top-performing teachers regardless of where they were trained. This may mean such schools would hire the top graduates from average programs, the average graduates from top programs, and no graduates from the weakest programs. In these schools all teachers would be about equal quality regardless of the quality of their preparation programs because selection offsets the program differences. The error terms would be strongly negatively correlated with program effects and associated indicators, violating the model assumptions and yielding biased estimates. We cannot fully test this possibility but we found a notable range in teacher licensure and SAT test scores in most schools with five or more recent graduates on staff during the study period.15 Hence, the available data do not support the conjecture of such restricted hiring based on information available to school administrators when they hire teachers. However, we do not have data on many other potential variables that may affect hiring, such as personality, student teaching reports, or transcripts, for example.

#### Inexperienced Teachers

Figure 4 shows the preparation program effects relative to the average program in Florida as well as the 95 percent confidence intervals for the estimates for three models: (1) no school controls, (2) with controls for school characteristics, and (3) with controls for school fixed effects.16 These results correspond to the preparation program coefficients (ρk) from equations 1, 2, and 3, respectively. The sample in these regressions is restricted to inexperienced teachers, and the outcome variable is the high-stakes SSS achievement test. The regression models include controls for student characteristics, teacher experience, as well as grade and year indicators. The preparation programs are ranked based on effectiveness according to the results from each estimation model.17

Figure 4.

Preparation Program Fixed Effects Regression Coeffcients and 95 Percent Confidence Intervals: Inexperienced Teachers

Figure 4.

Preparation Program Fixed Effects Regression Coeffcients and 95 Percent Confidence Intervals: Inexperienced Teachers

Close modal

There are a number of conclusions that can be drawn from these figures. First, although a large proportion of the preparation program estimates are statistically significantly different from zero from any one model, the precision of the estimates differs widely across models. In fact, of the thirty-three preparation programs, eight programs are significantly different (at the 95 percent confidence level) from the average in all three specifications, eight are significantly different from the mean in two of the three specifications, ten programs are significantly different from the mean in one specification, and seven programs are insignificantly different from the mean in all specifications.18 Second, the preparation program coefficient estimates vary to a large degree for some programs with the model specification. And finally, as more restrictive school controls are included in the models, the distribution of program effect estimates and confidence intervals increases.

Using table 6 we explore the changes in program rankings. The table displays the rankings of each preparation program based on the estimated coeffiecient and the quartile of the rankings for each specification. The preparation program rankings are sorted by the rankings from the specification without school characteristics.

Table 6.
Preparation Program Rankings and Ranking Quartiles: Inexperienced Teachers
Program IDRankRank QuartileRankRank QuartileRankRank Quartile
20
32 32
17
13
13
28
13 11
12 14 14
15 17
19 10
16 11 16 22
10 12 10 12
13 18 23
14 14 26 29
15 21 25
18 16 11
17 12 15
31 18
19 24 20
24 20
21 20 19
25 22 25 21
29 23 27 18
30 24 22 16
25 19 24
11 26 17 10
26 27 23
22 28 31 30
15 29 28 28
23 30 30 26
27 31 29 31
21 32 32 27
33 33 33 33
Program IDRankRank QuartileRankRank QuartileRankRank Quartile
20
32 32
17
13
13
28
13 11
12 14 14
15 17
19 10
16 11 16 22
10 12 10 12
13 18 23
14 14 26 29
15 21 25
18 16 11
17 12 15
31 18
19 24 20
24 20
21 20 19
25 22 25 21
29 23 27 18
30 24 22 16
25 19 24
11 26 17 10
26 27 23
22 28 31 30
15 29 28 28
23 30 30 26
27 31 29 31
21 32 32 27
33 33 33 33

Notes: Rankings based on program estimates in Appendix table A.1. Programs ordered by “No Schl Covars” rankings.

Policy makers may be interested in identifying the top-ranked preparation programs to scale up operations. To that effect, we consider the stability of the top quartile of preparation programs. There are three programs ranked in the top quartile under all three specifications. Of the remaining eleven programs in the top quartile under any specifications, seven preparation program change rankings from the top to at worst the second quartile, two preparation programs change rankings from the top to at worst the third quartile, and significantly, two programs change rankings from the top to at worst the bottom quartile.

Next we considered a similar exercise for a policy that targets the lowest quartile schools. For example, policy makers could wish to modify or terminate poor performing programs as suggested in the Department of Education's plan for teacher education reform. Six preparation programs are ranked in the bottom quartile in all specifications. Of the remaining five programs ranked in the bottom quartile for any specification, one program changes rankings to at best the third quartile, two preparation programs change rankings to at best the second quartile, and as mentioned earlier, two programs change rankings from the bottom to at best the top quartile.

Whereas so far we have focused on the preparation program effects, the sample used to estimate these effects includes all inexperienced elementary school teachers in the state, such as teachers who were certified out of state or obtained certifications through alternative pathways in Florida. The estimation model allows for comparisons of these two groups of teachers to one another. Teachers certified in Florida through alternative pathways are slightly more effective than teachers certified out of state in the no school effects specification. These coefficients are no longer significantly different from zero once school controls are included in the model, however.19

#### Teachers with All Levels of Experience

Figure 5 shows the preparation program effects for the three specifications on a sample that includes experienced elementary school teachers. Experienced teachers were excluded from the preparation program estimates in figure 4, but these teachers could affect estimates for the with-school-fixed-effects specification because they could have aided in identifying school effects. This is because non-recent graduates could provide a link between preparation programs that otherwise would not be linked in the preparation program/school network. Also, the school fixed effects are restricted to be the same for all teachers working at a given school, and this restriction could alter the parameter estimates in the model.

Figure 5.

Preparation Program Fixed Effects Regression Coefficients and 95 Percent Confidence Intervals: All Teachers

Figure 5.

Preparation Program Fixed Effects Regression Coefficients and 95 Percent Confidence Intervals: All Teachers

Close modal

The general conclusions about the three model specifications using the larger sample are very similar to earlier results. First, we note that under all specifications experienced teachers are more effective than inexperienced teachers who received out of state or alternative certification.20 When considering preparation program effects based on inexperienced teachers trained in Florida, a large number of programs are statistically different from the average program in Florida, but there is a significant change in the distribution of preparation program effects, the precision of the estimates, and the program rankings when comparing the three models.

Table 7 displays the rankings and ranking quartiles of preparation programs using all elementary school teachers in the Florida data set. Five preparation programs are ranked in the top quartile in all specifications. Of the remaining ten programs in the top quartile under any specifications, six programs change rankings from the top to at worst the second quartile, two programs change rankings from the top to at worst the third quartile, and two programs change rankings from the top to at worst the fourth quartile. Looking at the stability of the rankings across specifications in the bottom quartile, six programs are ranked in the bottom quartile under all specifications, two preparation programs are ranked in the second quartile at worst in another specification, two programs are ranked at worst in the third quartile in another specification, and two programs are ranked in the fourth quartile at worst in another specification.

Table 7.
Preparation Program Rankings and Ranking Quartiles: All Teachers
ProgramIDRankRankQuartileRankRankQuartileRankRankQuartile
20
32
17
10
28
13 12 10
12 13 15
15 17
19 10 16
11 19 22
16 12 17 19
14 13 25 26
10 14 14 13
31 15
16 23 24
18 17 27
18 16 18
19 26 23
24 20 11 14
25 21 27 25
22 24 20
29 23 20
30 24 11
25 22 21
11 26 21 12
26 27 18
22 28 31 29
15 29 29 28
23 30 30 31
27 31 28 32
21 32 32 30
33 33 33 33
ProgramIDRankRankQuartileRankRankQuartileRankRankQuartile
20
32
17
10
28
13 12 10
12 13 15
15 17
19 10 16
11 19 22
16 12 17 19
14 13 25 26
10 14 14 13
31 15
16 23 24
18 17 27
18 16 18
19 26 23
24 20 11 14
25 21 27 25
22 24 20
29 23 20
30 24 11
25 22 21
11 26 21 12
26 27 18
22 28 31 29
15 29 29 28
23 30 30 31
27 31 28 32
21 32 32 30
33 33 33 33

Notes: Rankings based on program estimates in Appendix table A.2. Programs ordered by “No Schl Covar” rankings.

When comparing the results from the two samples of teachers in figures 4 and 5, there are no differences in the model with no school characteristics. The program effects with school covariates vary more in the sample with all teachers, and in the school fixed effects specifications the rankings vary significantly across the two samples. This provides evidence that restricting the school effects to be the same for all teachers working at a given school regardless of experience does affect preparation program estimates. Twelve of the thirty-three preparation programs are ranked in different quartiles when comparing the estimation using only inexperienced teachers to the full sample for the school covariates model, and thirteen programs are ranked in different quartiles for the school fixed effect model.

### Variance Inflation

Variance inflation is a concern with models involving multiple sets of fixed effects such as preparation programs and schools.21 School fixed effects can be collinear with the program effects in the model when graduates of some programs never teach with graduates of other programs and groups of programs have many connections within the groups but few outside the group. Such multicollinearity can make the estimates of the program effects for some programs highly unstable and dependent on the students of very few teachers teaching in small numbers of schools.

Comparing the standard errors of the models with and without school fixed effects, the standard errors of twenty-eight out of thirty-three preparation programs are inflated in the with-school-fixed-effect estimation. This is partly because approximately 32 percent of the program graduates in the data teach in schools that employ only teachers from a single preparation program. These teachers do not contribute to the estimation of program effects in models with school fixed effects, although they would contribute in models with no school controls or with school covariates.

As shown in figure 6, the loss of these teachers can greatly inflate the standard errors of the estimated program effects for some programs. The figure plots the square root of the variance inflation factor for the estimated program effects against the percent of program graduates teaching in a school with graduates from only one program—that is, graduates lost in the school fixed effects analysis.22 The relationship is very strong with the percentage of graduates lost by including fixed effects explaining 63 percent of the variability in the variance inflation factor. Moreover, variance inflation from adding school fixed effects can be as large as 2.9, or 190 percent, and is over 1.5 for over 40 percent of the programs. Thus, the potential bias reduction from including school fixed effects comes at a very high price for a large percentage of the programs.

Figure 6.

Variance Inflation from Including School Fixed Effects

Figure 6.

Variance Inflation from Including School Fixed Effects

Close modal

The years of data used to estimate the program effects also has an impact on the variance inflation from including school fixed effects. Using a one- or two-year window results in an increase in the variance inflation factor to 3.7 for a one-year window, a nearly 50 percent increase over median variance inflation when we use a five-year window. Variance inflation for contrasts between programs increases similarly with reductions in the window length. The weakening of the network and the consequent increase in variance inflation from shortening the window is due to the decrease in the number of graduates in the programs where the medians fall from 25.5 to 10, the smaller number of schools where graduates are working, and the large increase in the proportion of graduates teaching in schools with graduates from a single program. With a one-year window, 50 percent of graduates from the median program are teaching at schools with graduates from a single program and will not contribute to program estimates from models with school fixed effects.

States like Florida that won the RTTT competition must provide measures of the performance of degree-granting teacher preparation programs in their states. One of the major concerns with such analyses is that program graduates may be teaching in very different contexts and those differences could be confounded with measures of the programs’ relative efficacy. This concern is exacerbated by the strong tendency for preparation program graduates to take jobs geographically close to the programs where they trained, potentially creating regional clusters of graduates. Models with school fixed effects would typically be seen as the best approach to removing potential confounding of context differences, because program estimates would rely on differences among student outcomes within the same schools to identify the program effects. Such estimates may not be feasible, however, if the training programs are not connected to each other. In addition, fixed effects estimates are consistent only under the assumption of homogeneity of effects, which may not hold if program effects differ in schools with teachers from multiple programs. This could occur if those schools are distinct from other schools or the program graduates drawn to work in them are distinct from the other graduates in their programs. Even if all the requirements for consistent fixed effects estimation hold, including school fixed effects in the models could inflate the variance of the estimates of program effects and contrasts between different programs. All the results are also likely to be sensitive to the number of school years for which school and program effects are assumed constant. Shortening the window will decrease the opportunities for graduates from different programs to be teaching in the same school and increase the challenges with using school fixed effects estimation to control for contextual differences among the working conditions for different program graduates. Finally, restricting the sample to only inexperienced teachers can also influence the preparation program coefficients and standard errors.

We used panel data from the 2000–01 to the 2004–05 school years linking teachers in Florida to their training programs and the schools where they teach to explore the potential for contextual bias and the feasibility of using school fixed effects when modeling teacher preparation program effects. We found strong evidence of regional clustering with program graduates significantly more likely to be working in schools geographically close to their training programs than ones far away. There were, however, enough graduates going far away and enough programs close together so that the network of programs was fully connected, provided we combined at least three years of data. Even with just one year of data the network of programs is fully connected, except for a few very small programs with one or two graduates each year. Thus, if desirable, school fixed effects would be feasible with a modest window or by restricting attention away from very small programs.

We also found that schools with graduates from a single program differed from other schools in terms of the demographics and achievement of their students. They tended to be smaller and to enroll smaller proportions of minority students, immigrant students, and students whose parents do not speak English. Students from schools with graduates from one program also tended to be higher achieving, but make smaller achievement gains. If these differences are not fully accounted for or unobserved differences in these distinct schools remain in the model, then program effects could be confounded, making models with school fixed effects highly desirable for protection against biases.

We found that the rankings of preparation programs based on relative effectiveness were significantly affected by the model specification for school context. Regardless of the sample we used in the analysis (all teachers or only inexperienced teachers), we found that at least one preparation program switched rankings from the top quartile to at worst the bottom quartile when school fixed effects were used. We observed that the rankings were more stable across specifications at the bottom of the ranking distribution than at the top, indicating the use of student growth models may be more effective at capturing low-performing programs than top tier programs.

We also found that the variance of the estimated program effects could be strongly inflated by including school effects in the model. Removing the potential for bias from the contextual effects of the schools with graduates from a single program is the primary motivation for using school fixed effects, but it will come at a cost. The cost is relatively insensitive to the window length provided three or more years of data are used for the analysis.

Our analyses suggest that if school fixed effects are desirable, a window of three years might provide an acceptable compromise between adding collinear variables and trying to protect against potential biases due to unobserved differences in the schools where graduates from different programs teach. With three years of data, variance inflation is not substantially larger than with the five-year window and school and program effects are assumed constant for three years rather than five. Given the tendency for schools and graduates that are influential for model identification to differ from other schools and graduates, it would be valuable to test for interactions between those observable differences and program effects.

There is no clean empirical method, however, to identify a model with no bias or a model that yields program effect estimates with the smallest mean squared error. States will need to make a choice on how to specify the student achievement growth model knowing that the choice may affect preparation program rankings and might be yielding a biased estimate unless untestable assumptions hold. In light of this evidence, states may need to consider if value-added modeling alone can provide useful information about preparation program effectiveness.

2

For the remainder of this article we refer to “preparation programs” as the institutions that train (and certify) teachers, and “schools” as the institutions where they teach after graduation.

3

An implicit assumption in this exercise is that teacher preparation programs can be validly compared based on the performance of the teachers they train. There are numerous concerns with this type of comparison, including selection of teachers into and out of programs, selection of program graduates into teaching positions within the state, and how teacher performance is measured. These issues are addressed in the Discussion section below.

6

For more details on teacher certification in Florida see Sass (2011).

7

A detailed analysis of the attributes and relative performance of teachers who obtain certification from pathways other than graduating from a Florida preparation program is provided in Sass (2011).

8

There are forty colleges and universities that certify teachers in the state of Florida. Four of these programs are excluded because they are part of the “Educator Preparation Institute” program, which is a type of alternative certification program. One program is excluded because all graduates were “business education” teachers, and are not certified to teach in elementary schools. Finally, two additional elementary teacher preparation programs do not appear in the analysis. These are small programs, with one or two recent graduates between 2000 and 2004 who are not teaching a fourth or fifth grade class during the analysis time period.

9

We exclude teachers who teach in charter schools, as well as teachers in classrooms with less than 10 or more than 50 students (loss of 112 teachers). Teachers are not included if all of their students are missing gain scores or demographic covariates (loss of 459 teachers).

10

These summary statistics are based on a sample of all teachers. Because in some model specifications many of these teachers are excluded, we examined whether the student and teacher characteristics of the estimation sample differ from the full sample, and found few statistically significant differences.

11

We use the Stata command felsdvregdm to estimate the program effects. For cases where the estimation sample includes all four groups of teachers, we specify two reference collections: one for inexperienced teachers certified in Florida preparation programs, and the second for the remaining teachers. This allows us to compare recent graduates relative to the average Florida preparation program even when teachers with more experience and other forms of certification are included in the data set.

12

A stratum or connected component is a maximal subset of the network in which all nodes are reachable from every other. Maximal means that it is the largest possible subgraph: You could not find another node anywhere in the graph such that it could be added to the subgraph and all the nodes in the subgraph would still be connected.

13

Figures available upon request.

14

This is based on the idea of communication flow, and the measure counts the number of shortest paths between all other nodes that pass through each node (Borgatti and Everett 2006). We use a version of the betweenness centrality index that takes into account the bimodal nature of our data, namely, that the network contains two types of entities, preparation programs and schools, and connections exist only between the two types of entities (preparation programs are only connected to one another through the schools where the teachers are employed) (Everett and Borgatti 2005). The two-mode centrality of the network is calculated using the social network analysis program UCINET, developed by Steve Borgatti, Martin Everett, and Lin Freeman, and available for download at www.analytictech.com/ucinet/.

15

We have two available measures of observed teacher quality in the data set: an indicator for whether the teacher passed the state licensure test on the first try and SAT test scores. We examined the frequency of first pass rates by subject, and found considerable variation in first pass rates within schools, with average school level first pass rates of 55 percent in math and 71 percent in reading. Similarly, there is considerable school-level variation in the SAT test scores. The average school-level range for test scores is 308 points on the 1200 scale SAT, and 80 percent of schools hired teachers who scored below 760 as well as above 995 on the SAT.

16

The average preparation program in Florida is normalized to zero in these regressions.

17

We also estimated these models using the low-stakes NRT exam as the outcome variable. When comparing across outcome variables for a specification, we found large differences in the results for the no-school-covariates model, but small changes in the coefficeints and resulting rankings in the school-fixed-effect model.

18

See Appendix table A.1 for preparation program effect coefficients and standard errors.

19

See Appendix table A.1 for coefficient estimates and standard errors.

20

See Appendix table A.2 for these results.

21

Other applications with multiple sets of fixed effects include students and teachers, workers and firms, or treatments and incomplete blocks.

22

Variance inflation equals the ratio of the variances of the estimators (program effects and contrasts) from a model with school fixed effects to the variances of the corresponding parameters from models without school fixed effects. The ratio is scaled by the ratio of the residual variances. Thus, variance inflation is a measure of the collinearity of the variables in the models and it is consistent with the traditional variance inflation factor (Belsley, Kuh, and Welsch 1980).

At the time of publication Daniel McCaffrey and J. R. Lockwood were employed by the Educational Testing Service, Princeton, NJ. This research was supported by an IES grant through a supplement to the National Center on Performance Incentives. The authors are grateful to the Florida Department of Education for providing the data. The views expressed are those of the authors and should not be attributed to the RAND Corporation, its trustees, or any of the funders or supporting organizations mentioned herein. Any errors are attributable to the authors.

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Table A.1.
Preparation Program Estimates and Standard Errors: Inexperienced Teachers
Program IDCoefs.e.Coefs.e.Coefs.e.
0.0018 0.0083 −0.0165* 0.0066 −0.0036 0.0089
0.0367* 0.0091 0.0223* 0.0077 0.0139 0.0102
−0.0064 0.0101 −0.0051 0.0091 0.0050 0.0125
0.0707* 0.0080 0.0271* 0.0068 0.0299* 0.0076
0.0207* 0.0083 0.0014 0.0069 −0.0088 0.0076
0.0116 0.0107 −0.0075 0.0096 −0.0269* 0.0120
0.0655* 0.0094 0.0437* 0.0084 0.0201* 0.0095
0.0051 0.0095 0.0275* 0.0083 0.0174 0.0114
−0.0157 0.0115 0.0010 0.0111 −0.0146 0.0147
10 0.0210* 0.0103 0.0305* 0.0094 0.0233* 0.0126
11 −0.0180 0.0124 0.0102 0.0117 0.0283* 0.0142
12 0.0374* 0.0169 0.0233 0.0167 0.0176 0.0209
13 0.0422* 0.0175 0.0280 0.0188 0.0393* 0.0207
14 0.0181 0.0149 −0.0287* 0.0157 −0.0400* 0.0163
15 −0.0592* 0.0198 −0.0568* 0.0204 −0.0390* 0.0221
16 0.0228 0.0171 0.0156 0.0167 −0.0056 0.0202
17 0.0801* 0.0308 0.0772* 0.0307 0.0764* 0.0348
18 0.0059 0.0248 0.0379 0.0258 0.0259 0.0332
19 0.0348 0.0266 0.0340 0.0271 0.0656* 0.0315
20 0.0984* 0.0254 0.0858* 0.0270 0.0438 0.0293
21 −0.1053* 0.0186 −0.1136* 0.0193 −0.0330 0.0234
22 −0.0466* 0.0225 −0.0836* 0.0243 −0.0616* 0.0260
23 −0.0705* 0.0226 −0.0823* 0.0230 −0.0314 0.0268
24 −0.0012 0.0215 0.0359* 0.0212 0.0533* 0.0267
25 −0.0089 0.0074 −0.0286* 0.0053 −0.0053 0.0070
26 −0.0272 0.0332 −0.0156 0.0331 0.0377 0.0427
27 −0.0928* 0.0288 −0.0776* 0.0339 −0.1358* 0.0312
28 0.0560* 0.0345 0.1277* 0.0345 0.1602* 0.0375
29 −0.0104 0.0492 −0.0418 0.0485 0.0070 0.0559
30 −0.0140 0.0493 −0.0092 0.0487 0.0166 0.0578
31 0.0046 0.1093 0.0673 0.0927 0.2165* 0.1032
32 0.0880 0.0565 0.1341* 0.0552 −0.1514 0.1129
33 −0.2454* 0.0593 −0.2638* 0.0576 −0.3409* 0.0634
InexpOutofStateCert. −0.0055* 0.0021 −0.0031 0.0022 −0.0022 0.0026
InexpAlternativeCert. 0.0055* 0.0021 0.0031 0.0022 0.0022 0.0026
Program IDCoefs.e.Coefs.e.Coefs.e.
0.0018 0.0083 −0.0165* 0.0066 −0.0036 0.0089
0.0367* 0.0091 0.0223* 0.0077 0.0139 0.0102
−0.0064 0.0101 −0.0051 0.0091 0.0050 0.0125
0.0707* 0.0080 0.0271* 0.0068 0.0299* 0.0076
0.0207* 0.0083 0.0014 0.0069 −0.0088 0.0076
0.0116 0.0107 −0.0075 0.0096 −0.0269* 0.0120
0.0655* 0.0094 0.0437* 0.0084 0.0201* 0.0095
0.0051 0.0095 0.0275* 0.0083 0.0174 0.0114
−0.0157 0.0115 0.0010 0.0111 −0.0146 0.0147
10 0.0210* 0.0103 0.0305* 0.0094 0.0233* 0.0126
11 −0.0180 0.0124 0.0102 0.0117 0.0283* 0.0142
12 0.0374* 0.0169 0.0233 0.0167 0.0176 0.0209
13 0.0422* 0.0175 0.0280 0.0188 0.0393* 0.0207
14 0.0181 0.0149 −0.0287* 0.0157 −0.0400* 0.0163
15 −0.0592* 0.0198 −0.0568* 0.0204 −0.0390* 0.0221
16 0.0228 0.0171 0.0156 0.0167 −0.0056 0.0202
17 0.0801* 0.0308 0.0772* 0.0307 0.0764* 0.0348
18 0.0059 0.0248 0.0379 0.0258 0.0259 0.0332
19 0.0348 0.0266 0.0340 0.0271 0.0656* 0.0315
20 0.0984* 0.0254 0.0858* 0.0270 0.0438 0.0293
21 −0.1053* 0.0186 −0.1136* 0.0193 −0.0330 0.0234
22 −0.0466* 0.0225 −0.0836* 0.0243 −0.0616* 0.0260
23 −0.0705* 0.0226 −0.0823* 0.0230 −0.0314 0.0268
24 −0.0012 0.0215 0.0359* 0.0212 0.0533* 0.0267
25 −0.0089 0.0074 −0.0286* 0.0053 −0.0053 0.0070
26 −0.0272 0.0332 −0.0156 0.0331 0.0377 0.0427
27 −0.0928* 0.0288 −0.0776* 0.0339 −0.1358* 0.0312
28 0.0560* 0.0345 0.1277* 0.0345 0.1602* 0.0375
29 −0.0104 0.0492 −0.0418 0.0485 0.0070 0.0559
30 −0.0140 0.0493 −0.0092 0.0487 0.0166 0.0578
31 0.0046 0.1093 0.0673 0.0927 0.2165* 0.1032
32 0.0880 0.0565 0.1341* 0.0552 −0.1514 0.1129
33 −0.2454* 0.0593 −0.2638* 0.0576 −0.3409* 0.0634
InexpOutofStateCert. −0.0055* 0.0021 −0.0031 0.0022 −0.0022 0.0026
InexpAlternativeCert. 0.0055* 0.0021 0.0031 0.0022 0.0022 0.0026

Note: Models include student characteristics, teacher experience measures, as well as grade and year indicators.

*Statistically significant at the 5% level.

Table A.2.
Preparation Program Estimates and Standard Errors: All Teachers
Program IDCoefs.e.Coefs.e.Coefs.e.
0.0014 0.0081 −0.0342* 0.0064 −0.0268* 0.0071
0.0353* 0.0088 0.0032 0.0075 −0.0127 0.0080
−0.0095 0.0099 −0.0261* 0.0087 −0.0186* 0.0101
0.0732* 0.0078 0.0156* 0.0063 0.0179* 0.0064
0.0216* 0.0081 −0.0131* 0.0066 −0.0245* 0.0066
0.0092 0.0104 −0.0252* 0.0093 −0.0313* 0.0101
0.0659* 0.0092 0.0296* 0.0079 0.0158* 0.0082
0.0037 0.0093 0.0026 0.0080 −0.0168* 0.0093
−0.0177 0.0112 −0.0199* 0.0106 −0.0226* 0.0121
10 0.0201* 0.0101 0.0118 0.0090 0.0070 0.0100
11 −0.0190 0.0121 −0.0154 0.0113 0.0077 0.0122
12 0.0383* 0.0165 0.0123 0.0162 −0.0026 0.0180
13 0.0388* 0.0171 0.0125 0.0183 0.0135 0.0177
14 0.0208 0.0146 −0.0319* 0.0152 −0.0409* 0.0147
15 −0.0577* 0.0193 −0.0776* 0.0198 −0.0444* 0.0203
16 0.0211 0.0167 −0.0002 0.0162 −0.0186 0.0175
17 0.0807* 0.0301 0.0734* 0.0300 0.0935* 0.0318
18 0.0066 0.0243 0.0244 0.0251 −0.0442* 0.0269
19 0.0327 0.0260 0.0262 0.0264 −0.0092 0.0282
20 0.0963* 0.0248 0.0785* 0.0264 0.0445* 0.0265
21 −0.1061* 0.0182 −0.1249* 0.0188 −0.0818* 0.0198
22 −0.0459* 0.0220 −0.0921* 0.0237 −0.0689* 0.0233
23 −0.0709* 0.0220 −0.0878* 0.0224 −0.0870* 0.0230
24 −0.0031 0.0210 0.0150 0.0207 0.0006 0.0232
25 −0.0087 0.0072 −0.0456* 0.0050 −0.0354* 0.0056
26 −0.0219 0.0325 −0.0106 0.0323 0.0170 0.0368
27 −0.0931* 0.0281 −0.0709* 0.0330 −0.1487* 0.0297
28 0.0568* 0.0337 0.1170* 0.0336 0.1468* 0.0353
29 −0.0155 0.0480 −0.0144 0.0473 0.0327 0.0500
30 −0.0160 0.0482 0.0172 0.0475 0.0080 0.0525
31 0.0130 0.1067 0.2775* 0.0898 0.4262* 0.0971
32 0.0899 0.0552 0.1749* 0.0538 0.1705* 0.1029
33 −0.2403* 0.0579 −0.2015* 0.0562 −0.2668* 0.0590
InexpOutofStateCert. −0.0298* 0.0023 −0.0270* 0.0023 −0.0243* 0.0025
InexpAlternativeCert. −0.0152* 0.0025 −0.0153* 0.0025 −0.0174* 0.0026
ExperiencedTeachers 0.0450* 0.0023 0.0423* 0.0024 0.0416* 0.0024
Program IDCoefs.e.Coefs.e.Coefs.e.
0.0014 0.0081 −0.0342* 0.0064 −0.0268* 0.0071
0.0353* 0.0088 0.0032 0.0075 −0.0127 0.0080
−0.0095 0.0099 −0.0261* 0.0087 −0.0186* 0.0101
0.0732* 0.0078 0.0156* 0.0063 0.0179* 0.0064
0.0216* 0.0081 −0.0131* 0.0066 −0.0245* 0.0066
0.0092 0.0104 −0.0252* 0.0093 −0.0313* 0.0101
0.0659* 0.0092 0.0296* 0.0079 0.0158* 0.0082
0.0037 0.0093 0.0026 0.0080 −0.0168* 0.0093
−0.0177 0.0112 −0.0199* 0.0106 −0.0226* 0.0121
10 0.0201* 0.0101 0.0118 0.0090 0.0070 0.0100
11 −0.0190 0.0121 −0.0154 0.0113 0.0077 0.0122
12 0.0383* 0.0165 0.0123 0.0162 −0.0026 0.0180
13 0.0388* 0.0171 0.0125 0.0183 0.0135 0.0177
14 0.0208 0.0146 −0.0319* 0.0152 −0.0409* 0.0147
15 −0.0577* 0.0193 −0.0776* 0.0198 −0.0444* 0.0203
16 0.0211 0.0167 −0.0002 0.0162 −0.0186 0.0175
17 0.0807* 0.0301 0.0734* 0.0300 0.0935* 0.0318
18 0.0066 0.0243 0.0244 0.0251 −0.0442* 0.0269
19 0.0327 0.0260 0.0262 0.0264 −0.0092 0.0282
20 0.0963* 0.0248 0.0785* 0.0264 0.0445* 0.0265
21 −0.1061* 0.0182 −0.1249* 0.0188 −0.0818* 0.0198
22 −0.0459* 0.0220 −0.0921* 0.0237 −0.0689* 0.0233
23 −0.0709* 0.0220 −0.0878* 0.0224 −0.0870* 0.0230
24 −0.0031 0.0210 0.0150 0.0207 0.0006 0.0232
25 −0.0087 0.0072 −0.0456* 0.0050 −0.0354* 0.0056
26 −0.0219 0.0325 −0.0106 0.0323 0.0170 0.0368
27 −0.0931* 0.0281 −0.0709* 0.0330 −0.1487* 0.0297
28 0.0568* 0.0337 0.1170* 0.0336 0.1468* 0.0353
29 −0.0155 0.0480 −0.0144 0.0473 0.0327 0.0500
30 −0.0160 0.0482 0.0172 0.0475 0.0080 0.0525
31 0.0130 0.1067 0.2775* 0.0898 0.4262* 0.0971
32 0.0899 0.0552 0.1749* 0.0538 0.1705* 0.1029
33 −0.2403* 0.0579 −0.2015* 0.0562 −0.2668* 0.0590
InexpOutofStateCert. −0.0298* 0.0023 −0.0270* 0.0023 −0.0243* 0.0025
InexpAlternativeCert. −0.0152* 0.0025 −0.0153* 0.0025 −0.0174* 0.0026
ExperiencedTeachers 0.0450* 0.0023 0.0423* 0.0024 0.0416* 0.0024

Note: Models include student characteristics, teacher experience measures, as well as grade and year indicators.

*Statistically significant at the 5% level.