Abstract
Relative to defined benefit (DB) plans, defined contribution (DC) plans have been linked to greater employee mobility. Because employees with different underlying mobility tendencies may sort across plans or firms, the relationship between plan type and mobility may be due to selection. We identify the role of selection by exploiting a natural experiment at an employer, in which the transition from a DB to a DC pension plan was affected by default rules. Using the default assignment as a source of exogenous variation in plan enrollment, we find that employees with higher mobility tendencies self-select into the DC plan.
I. Introduction
We identify the role of selection in the context of retirement plans and employee mobility. Although our setting is an employer undergoing a plan transition, it is informative about the relationship between two broader labor market trends: first, the change in the pension plan landscape and second, increased employee mobility. Among private sector employees in the United States with an employer-provided pension plan, the fraction covered solely by a defined contribution (DC) plan more than tripled between 1980 and 2003, while those covered solely by a defined benefit (DB) plan declined by over 80 percent (Buessing and Soto 2006). Concurrently, employee job tenure and retention rates have decreased (Munnell, Haverstick, and Sanzenbacher 2006; Farber 2007; Friedberg and Owyang 2005). It is commonly thought that the increase in DC plans has played a role in the increase in mobility because DB and DC plans typically differ in how employee tenure relates to pension wealth. In particular, pension-wealth accrual is typically more backloaded in DB plans relative to DC plans, which acts to reduce the relative portability of DB plans (Mitchell 1982; Lazear 1990). Although DB plans and DC plans differ in multiple dimensions, such as control of financial decision-making, access to liquidity, and the transparency of wealth accrual, difference in the portability of the plans naturally has been the focus when relating plan type to mobility trends.
Researchers have shown that employees in DB plans tend to have longer tenure relative to those in DC plans (Munnell, Haverstick, and Sanzenbacher 2006; Friedberg and Owyang 2005). However, the selection of employees across plans may drive part of any observed relationship between mobility patterns and pension plan type. Understanding the causal effect of pension plan type on turnover requires estimating the direct effect of plan features on employee turnover, which we refer to as an incentive effect, separate from the selection effect, defined as differences in turnover that stem from the underlying correlation between mobility tendencies and preferences for plan characteristics. However, disentangling the incentive effect from the selection effect has typically been challenging because it requires comparing mobility across employees who are enrolled in different plans but are otherwise similar.
This paper identifies the role of selection in the relationship between employee mobility and pension plan type by exploiting a natural experiment at a single employer in which existing employees faced a one-time, irrevocable option to transition from a DB plan to a DC plan. Separating the direct effects of program participation from the effects generated by selection into participation has been a topic of interest in many different contexts yet is typically challenging to achieve due to a lack of random assignment. We exploit exogenous variation in the probability of switching to the DC plan caused by a default rule that governed the plan transition. In particular, existing employees who were under age 45 at the time of the transition were assigned the DC plan as the default plan, while employees aged 45 or older were assigned the DB plan as the default plan. Default rules have been shown to have dramatic effects on DC enrollment (Madrian and Shea 2001), and this result holds across a variety of private employment contexts (Choi et al. 2004) as well as in public-sector pension plans (Cronqvist and Thaler 2004). Furthermore, Goda and Manchester (2013) find that the effect of defaults on retirement plan choice is similarly powerful.1
We use the default retirement plan rules as an instrument for DC enrollment in order to overcome selection bias and identify the effect of plan type on employee mobility. We conduct a difference-in-differences (DD) estimation strategy that uses data before and after the plan transition and leverages the difference in default plan for employees under and over age 45 to isolate the role of selection. Although conceptually the features of the default rule governing the plan transition point to the use of regression discontinuity estimation methods, empirically we have limited power to implement this technique due to the combination of low baseline mobility rates and a limited number of employees in the narrow window around age 45.2 We sign the selection effect by comparing simple probit estimates, which are confounded by employee selection, to selection-corrected estimates. We find evidence that our simple probit estimates are significantly less than the selection-corrected estimates for one-, two-, and three-year mobility outcomes. These findings provide evidence that employees with higher mobility tendencies select into the DC plan over the DB plan.
This paper contributes to the literature on pension plan type and mobility in three ways. First, the paper provides a new source of identification with which to quantify the role of selection into pension plans based on mobility. Prior studies have generally addressed this selection by using selection-correction models or cross-sectional data that includes heterogeneous firms and plans (Allen, Clark, and McDermed 1993; Gustman and Steinmeier 1993; Rabe 2007). Other studies have used plausibly exogenous variation from tax reforms (Andrietti and Hilderband 2004) or plan offerings (Disney and Emmerson 2004; Manchester 2010) to identify the consequences of pension plan type for mobility. Our approach uses exogenous variation induced by the default rule governing the plan transition in a DD framework. This technique relies on the assumption that before and after the policy change, trends in unobservable determinants of mobility for affected employees relative to unaffected (but otherwise similar) employees did not differ on either side of the age governing the default plan. Our identifying assumption passes falsification tests that generally show no evidence of differential mobility on either side of alternative age thresholds or in years prior to the policy change. We also confirm that no one particular year of data from the preperiod is driving the results.
Second, we develop a conceptual framework for evaluating the effect of introducing a new benefit on mobility that allows for heterogeneity in preferences over the benefit, costs of switching, and mobility costs. We show that the resulting relationship between benefit enrollment and mobility depends on the joint distribution of this multidimensional heterogeneity as well as the choice environment in which the new benefit is offered. In particular, whether employees have the opportunity to self-select into the new benefit as compared to being forced to enroll has different implications for observable mobility patterns across plans. We use both of these insights to generate testable predictions for our estimated parameters and to provide a richer interpretation of our empirical evidence.
This framework sheds new light on previous findings of pension plans and employee mobility. In particular, some previous evidence has shown that both DB and DC plans may reduce employee mobility. It has been hypothesized that this result is due to compensation premiums for employees with a pension plan relative to those without (Gustman and Steinmeier 1993), and the possibility that the retention effect is driven by preferential treatment of savers by employers (Ippolito 2002). While Aaronson and Coronado (2005) theorize that changes in employee benefit demand may have driven, at least in part, the transition from DB to DC plans, they do not present a conceptual model or empirical strategy for isolating a selection effect. Our framework implies that the overall effect of plan type on mobility depends on the sign and magnitude of the incentive and selection effects.
Applying this framework to our setting, we find that the selection effect induces a positive relationship between mobility and endogenous DC plan enrollment. Interestingly, the DC plan is not associated with higher turnover once we account for this selection effect—that is, exogenous assignment to theDC plan reduces mobility relative to the DB plan. This finding highlights the possibility that employees find the bundle of DC plan features, including increased control, transparent wealth accrual, and loan and withdrawal provisions, desirable relative to those of the DB plan (as measured by higher retention), which is in line with previous work that finds a low perceived benefit of additional DB benefits (Fitzpatrick 2015; Brown et al. 2011).
Third, we are able to evaluate both the short-term and longer-term effects of DC plans on mobility as our data extends to three years beyond the DC plan introduction. With the exception of Allen, Clark, and McDermed (1993), most studies evaluating the relationship between pension plan and mobility use a one-year time frame (Gustman and Steinmeier 1993; Andrietti and Hilderband 2004; Disney and Emmerson 2004; Rabe 2007). We find that the pattern of positive selection effects and negative incentive effects are consistent across the one-, two-, and three-year time horizons for measuring mobility.
Our results are specific to our context and the specific features of the DB and DC plans under consideration. However, there are reasons to suggest that our results are more generally relevant for a number reasons. First, one key difference between the DB plan in our context and the standard DB plan is that the benefit formula in our setting is less backloaded, which weakens the relationship between tenure and pension wealth accrual. This feature biases us against finding evidence of positive selection into DC plans based on mobility tendencies relative to a setting with a more standard DB plan. Second, the theoretical framework can be applied to traditional DB plans and to employer provided benefits beyond retirement plans, and our framework provides intuition as to how results may vary with changes in the setting. Third, the employer we study, a large private university, includes a range of employees across occupations and job categories, including service workers, technical employees, and skilled and unskilled positions.
The remainder of the paper proceeds as follows. Section II describes the conceptual framework that motivates our empirical approach and examines what our results may reveal about the relationship between mobility tendencies and pension plan preferences. Section III provides details regarding the natural experiment we exploit in our empirical application. We outline our empirical strategies in Section IV and present our results along with robustness checks in Section V. Section VI explores the implications of our results and concludes the paper.
II. Model of New Benefit Enrollment and Mobility
We construct a conceptual framework for interpreting observational and quasi-experimental estimates of the relationship between mobility patterns and employee benefit enrollment in the presence of unobservable heterogeneity. To do this, we first propose a basic framework that describes individual decisions regarding enrollment in a newly offered benefit and subsequent turnover. Second, we evaluate the observable implications of this framework in two distinct choice scenarios for benefit enrollment: one where benefit enrollment is endogenously chosen and one where it is exogenously determined. Finally, we show how comparing the relationship between new benefit enrollment and turnover in these two scenarios provides insight into the selection effect (that is, the relationship between underlying mobility tendencies and preferences for the new benefit).3
We model the discrete decision between a new employer-provided benefit and an existing one and the subsequent decision to leave or stay with one’s current employer. An employee in our model, indexed by i, has three sources of individual-level heterogeneity: ϕi, which determines her relative valuation of the new employee benefit over the old option; ci > 0, which represents the employee’s cost of switching to the new employee benefit; and mi, which dictates the mobility tendencies associated with switching to a new employer. These three sources of heterogeneity are governed by a joint distribution with CDF F(.) : R3→[0, 1].
We will map these unobservable parameters into empirical outcomes. We define Bi to be a binary variable indicating enrollment in the new benefit at one’s current employer and Li, for “Leaving,” to be a binary variable indicating departure from the current employer. For example, in our setting Bi = 1 indicates that an employee is observed enrolled in the DC retirement plan rather than the DB plan, while Li = 1 indicates that an individual has subsequently left the firm within one, two, or three years of being initially observed.4
An employee maximizes her expected utility, E[Vi(wi, Bi)], which, among other things, depends on the employee’s wagewi, the status of her benefit participation Bi, and her choice of employer. We begin with the benefit enrollment decision. The parameter ϕi, which captures the net utility change of enrolling in the new benefit, is defined as follows:

Employees with a higher ϕi place a higher value on the new benefit. In our context, such employees may prefer a DC plan to aDB plan for a number of reasons, including the net present value, the risk profile of the retirement plan, transparency, portability, and control over investment.
When enrollment is determined solely by the employee, she must pay a cost of switching to the new benefit, ci > 0, in order to realize this utility change. This may include such costs as time, informational requirements, or administrative hurdles associated with switching benefits. It follows that the employee will use the following decision rule for adoption of the new benefit:

We now turn to the decision of whether to leave the firm. Denote
as the value of working at an outside firm and ηi as a cost of switching employers. We definemi as the net benefit of leaving the current employer for an outside employer, conditional on having the old benefit:

Thus, individuals with a higher mi are more “mobile,” in that their outside options tend to be better relative to the current employer and/or they tend to have lower switching costs across employers. The decision to leave the firm can be characterized as follows:

It may seem that we have suppressed the dynamic nature of the these two decisions made at different points in time. However, we have placed little restriction on the joint distribution of (ϕi, mi, ci). Thus, the correlation between these reduced-form parameters can capture forward-looking behavior. For example, agents with a high likelihood of leaving the firm—that is, a high mi—may generally have a low value of enrollment— that is, ϕi is low relative to ci—because they will not be at the firm for long.
We also have assumed that the benefit does not directly affect utility at outside firms. This may be violated when a new benefit is more portable than the old, as is typically the case with DC plans. We discuss in more detail in Appendix 1C the case where this phenomenon is captured by having the benefit directly affect the cost of switching—that is, ηi = ηi(Bi). In our particular setting, the DB plan is less backloaded than typical DB plans, and thus our simplification may be less of a concern. Additionally, we replicate our results in Appendix 3B among a sample of employees who would be vested under either the DB or DC plan, which further reduces any discrepancies in portability.
We now consider two choice scenarios. In the first case, Bi is endogenously determined by the employees, and the default policy is a DB plan. In this case, enrollment is determined according to Equation 2. In the second case, benefit enrollment is exogenously determined by the employer. In each case, we discuss the association between benefit enrollment and observed mobility and how these relationships may be informative about the joint distribution of (ϕi, mi, ci). In particular, we are interested in the comovement of preferences for the new benefit, ϕi, and mobility, mi.
In the endogenous case, the employer introduces a new benefit and allows employees to select into this benefit according to the rule in Equation 2. Subsequently, employees make a decision on whether or not to leave the firm according to the rule in Equation 4. Consider a comparison of the subsequent leave probabilities among those enrolled and those not enrolled. We define this difference as:

where the “Endo” subscript denotes endogenously determined benefit enrollment.5 We have decomposed this observed difference into a treatment on the treated (β1) and a selection effect (βSelection). The treatment on the treated can be interpreted as the treatment effect among those who enroll, that is, those for whom Bi = 1 in Equation 2. The selection effect is the baseline difference in Li between those who enroll when given the choice (that is, Bi = 1) and those who do not (that is, Bi = 0).
To build intuition regarding this decomposition, note that those who have chosen to enroll (that is, Bi = 1) must have a positive value of ϕi, given Equation 2 and the assumption that ci > 0. Focusing just on the left-hand sides of the inequalities in Equation 4, those now enrolled have less of a reason to leave the firm relative to those not enrolled, all other things equal. That is, ϕi $ Bi > 0 for enrollees. We refer to this direct effect of the new benefit on the likelihood of leaving, β1, as the “incentive effect.”
In our context, a negative incentive effect means that the DC plan reduces turnover relative to the DB plan among those choosing to enroll in the new DC benefit. This may seem counterintuitive given that DC plans are typically more portable. However, recall that the parameter ϕi captures preferences for the multidimensional differences between a DC plan and DB plan. All things equal, those who value the DC plan more receive higher utility in the job now that it has a DC plan and are therefore less likely to leave it.
We now turn to the second component of the decomposition in Equation 5. Focusing on the right-hand sides of the inequalities in Equation 4, the difference in leave probabilities between enrollees and nonenrollees will depend on differences in the distribution of mi across the two groups. We refer to the difference in leave probabilities due to differences in the distribution of mi between enrollees and nonenrollees as the “selection effect” or βSelection. The sign of the selection effect depends on the baseline difference in leave probabilities absent the new benefit.
Now consider the second-choice scenario, where benefit enrollment is exogenously determined. Imagine comparing the probability of leaving the firm under the new benefit regime as compared to under the original regime. The decision to leave the firm is still dictated by the decision rule in Equation 4. However, now that employees are not self-selecting into the new benefit, we no longer have a selection effect since plan enrollment is independent of m. Furthermore, because there is no endogenous enrollment into Bi, it is no longer the case that ϕi $ Bi > 0 for all enrollees. Instead, the incentive effect will vary across employees, decreasing the likelihood of leaving among those who have a positive ϕi and increasing the likelihood of leaving for those with a negativeϕi. The net change in leave probabilities depends on the number of employees now induced to stay with the firm—that is, those with mi and ϕi such that 0 < mi ≤ ϕi—relative thosewho are now induced to leave the firm—that is, those with mi and ϕi such that 0 ‡mi >ϕi.
A comparison of leave probabilities under the new relative to the old benefit regime identifies the average incentive effect of Bi among all employees, or a treatment effect defined as:6

Note, we have decomposed the treatment effect into an effect among employees who would enroll endogenously (that is, Bi = 1) and those who would not (that is, Bi = 0). The incentive effect β1 is the treatment on the treated, defined previously in Equation 5, while the incentive effect β0 is an analogous treatment on the untreated. The weights π0 and π1 are the population shares of the two respective types.
Now that we have defined the estimates for the endogenous and exogenous cases, we can show how the characteristics of the (ϕi, mi, ci) distribution are related to the relative magnitude of the estimates. Fixing ci = c, suppose that mi and ϕi are independent, meaning there is no selection effect. This means that the distribution ofmi does not differ among those who choose to enroll in the new benefit under the endogenous case and under the exogenous case. If there is no selection effect, then we would expect to find a larger reduction in leave probabilities under the endogenous case than the exogenous case (that is, βEndo < βExog). This is because those who self-select into the new benefit have weakly higher values for the benefit, and therefore experience larger reductions in the probability of leaving due to the incentive effect, all things equal.7 Now, suppose that the selection effect is negative. This scenario would further reduce βEndo relative to βExog because the negative selection effect would reinforce the negative incentive effect present in the endogenous case, again implying βEndo < βExog. Finally, a positive selection effect would offset the difference between the endogenous and exogenous estimates, potentially even reversing the relative magnitude of βEndo and βExog.
In Appendix 1B we formally show in Proposition 1 that if we are able to observe the relationship between plan enrollment and leaving in these two settings, we can learn something about the role of selection. In particular, the selection effect is bounded from below by the difference between the relationship estimated in endogenous and exogenous settings:

To see why this is the case, substitute for βEndo and βExog using Equations 5 and 6 as follows:

We argue in the appendix that the second term in Equation 8 is negative, thus establishing the lower bound on βSelection. We cannot directly verify the assumption that β1 – β0 < 0. For benefits that primarily affect payoffs during employment with the current firm, such as health insurance, it makes sense to assume that the new benefit is less likely to make those who would actively choose the benefit to leave the firm than those who would not choose the benefit. As discussed above, one potentially relevant violation of our assumption is the case where the new benefit directly affects the cost of leaving the firm through, for example, greater portability. In our context, however, it happens to be the case that the DB plan is less backloaded than typical DB plans, and therefore, this may be less of a concern.
Importantly, Equation 7 shows that the key test for positive selection is asymmetric in that a negative or zero difference (that is, βEndo ≤ βExog) is not informative about the sign of the selection effect.8 This is because the selection effect could reinforce or counteract the incentive effect. Only in the case where the exogenous estimates show a larger reduction in leave probabilities than the endogenous estimates (that is, βEndo > βExog), can we rule out a zero or negative selection effect in favor of a positive selection effect. A regression of mobility (Li) on newbenefit enrollment among employees who can choose their benefit approximates the endogenous case. As shown above in Equation 5, the correlation between Li and Bi in this choice scenario is driven by both the incentive effect and the selection effect. Estimating the effect of new benefit enrollment on leave probabilities when benefit enrollment is randomly assigned approximates the exogenous case (that is, Equation 6).9 The effect of Bi on Li in that case identifies the average incentive effect. The resulting estimates can then be used to evaluate the key inequality in Equation 7.
III. Institutional Setting and Data
A. Setting
We use data on unionized, nonfaculty employees from a large research university. Although our data are from a single institution, the jobs represented in the sample are diverse, ranging from those with lowskill requirements (for example, athletic equipment keeper, food service worker) to relatively high-skilled jobs (for example, life science technician, computer service, audio equipment specialist). These employees underwent a retirement plan transition on September 1, 2002. Existing employees in this group could elect to continue participating in the DB plan, or choose to move to the DC plan and cease accruing benefits under the DB plan.10 Our analysis is restricted to these existing employees. If no election was made, the employee was enrolled in the default plan. The default plan depended on the employee’s date of birth. In particular, employees under age 45 as of September 1 were assigned the DC plan as the default, while employees age 45 or older as of September 1 were assigned the DB plan as the default.11
The DB plan at the employer offered benefits equal to 2 percent of an employee’s average salary, multiplied by the total years of service. Because the benefit base was the average salary rather than a final average salary based on the three or five years prior to retirement, DB benefit accruals were less backloaded than is typically the case with DB plans. These benefits were vested for employees with at least five years of service. The DC plan offered a 5 percent employer contribution and matching schedule up to an additional 5 percent.12 Employer contributions to the DC plan were considered vested immediately for employees in our sample.
How does our setting compare to other employers? One key difference between the DB plan in our context and the standardDB plan is that the benefit formula in our setting is less backloaded, which weakens the relationship between tenure and pension wealth accrual. In addition, our university setting is not typical in that the benefits and working conditions are likely superior to other private sector employers. Given this, the employees in our sample are likely to have lower underlying mobility tendencies than most private sector employees. Moreover, other benefits (such as healthcare and education benefits) may mitigate employees’ responses to any change in one particular benefit. We expect that both of these factors would bias us against finding evidence of positive selection into DC plans based on mobility tendencies.
An important dimension to consider when evaluating the effects of the plan transition on employee mobility is the relative generosity of the two plans. Because of differences in how pension wealth accrues, the relative value of the two plans depends on employee characteristics, such as risk preference, financial literacy, and mobility tendencies as well as the performance of financial markets. Goda and Manchester (2013) carefully evaluate the value of the two plans by comparing the certainty equivalents under a baseline set of assumptions and show that, among low levels of risk-aversion, the plans are of comparable value around age 45, the DC plan is more valuable to younger employees, and the DB plan is more valuable to older employees. For higher levels of risk-aversion, the DB plan has a higher certainty equivalent than the DC plan across all ages.
B. Data
We construct an original data set using administrative data from two sources: annual payroll records that include employees present at the university on December 15 of each year from 1999 to 2005 and pension plan records. The payroll data includes annual information on job, salary, and weekly hours worked as well as demographic characteristics, including exact date of birth, gender, race, and hire date.13 Pension plan records include information on annual plan enrollment as well as which plan was the default plan for employees who were eligible for the plan transition. Our outcome measures are binary variables that indicate whether an employee we observe in year t is present in the dataset in a future year for one-, two-, and three-year time horizons. As such, it measures the probability of leaving the employer, either voluntarily or involuntarily, within one, two, or three years.
While conceptually the variation in default plan by age aligns well with a regression discontinuity approach, our power is limited due to lowbaseline leave propensities and a relatively small sample size.14 Instead, we employ a DD method using data from the transition year (2002) and years prior to the transition (1999–2001). Table 1 reports summary statistics for the sample broken out by the relevant differences used in the analysis. Column 1 reports summary statistics for employees in all years and for all ages. Columns 2 and 3 report descriptive statistics for employees under 45 and employees 45 and older, respectively, for the pretransition years, while Columns 4 and 5 show this same comparison for the transition year. Comparing the leave propensities across the columns, the data show a sizable drop in leave propensities among the under 45 employees (Column 2 vs. 4, while mobility rates for employees age 45 and over are relatively stable over this time period (Column 3 vs. 5). At the same time, the second row of Table 1 shows how DC enrollment went up dramatically for employees under age 45. Figure 1 plots one-year mobility and DC enrollment by year for these same two employee groups. Both employees above and below age 45 experienced a drop in mobility in 2001, prior to the plan transition. However, while the mobility of employees under age 45 (who became enrolled in the DC plan to a greater degree) continued to decline, the mobility of those over 45 increased slightly in 2002 following the plan transition. Overall, these descriptive results suggest that employees who ended up in the DC plan exhibited a greater decrease in leave propensities relative to employees who remained in the DB plan.
Notes: Over 45 represents employees age 45 or older on September 1, 2002. Under 45 represents employees younger than age 45 on September 1, 2002. Employees over 45 were defaulted to remain in the DB plan for 2002 and later, while employees under 45 were defaulted to switch to the DC plan.
IV. Empirical Strategy
We quantify the role of selection as outlined in Section II by estimating the endogenous and exogenous relationship between enrollment in the DC plan and mobility albeit with one difference. Rather than true random assignment as described in Section II, we exploit the variation in DC enrollment produced by the different default plan for employees on either side of age 45 in 2002. In the following, we describe our empirical strategy and how the resulting estimates map to Equation 7, which is the key inequality from our model.
Because we have a binary outcome with a mean relatively close to zero, we rely on a probit specification.15

where Li is a binary variable that equals 1 if the employee is not with the employer one year later. We also consider specifications that measure leaving two and three years later. The variable DCi is a dummy equal to one if employee i is in a DC plan. The variable Post2002i is an indicator for being observed in the year 2002, and the variable Under45i is a binary variable that takes the value 1 if the employee is younger than age 45 on September 1, 2002.16 The vector Xi consists of demographic control variables for gender, race, hours, base salary, and tenure at the employer and dummies for department. We also include specifications where Xi includes a series of age and year dummy variables, omitting Post2002i and Under45i, to control more flexibly for age and year. Finally,
is an unobserved factor related to mobility. We first consider the following naïve probit specification of Li on DCi, Post2002i, Under45i and Xi:

In our caseDCi may be an endogenous regressor, that is DCi and ui may be correlated, resulting in a biased coefficient on DCi. We define βEndo as the average partial effect of DCi on Li, estimated from this endogenous regression:

In order to address the endogeneity issue, we apply a control function approach, sometimes referred to as Two-Stage Residual Inclusion (or 2SRI, Terza, Basu, and Rathouz 2008), using default retirement plan rules as an instrument for DC enrollment. Specifically, our instrument for DC enrollment is the interaction term Post2002i × Under45i. Recall that this group has the DC plan as the default retirement plan in 2002. We briefly summarize the procedure here and show in more detail in Appendix 2 how this method allows us to overcome the endogeneity. In the first stage, we estimate the effect of the default provision on DC participation for those under 45 in 2002 relative to those over 45 in 2002 using a linear model. In the second stage, we estimate the effect of DC participation on the one-year turnover probability while including the residual from the first stage. Our first stage regression is as follows:

The residual from the first stage regression in Equation 12 is then included as a control function in the following probit specification:

We define βExog as the average partial effect estimated using the parameters in Equation 13:

To gain further intuition into our approach, note that if we were to specify a linear probability model instead of a probit model, this control function method would be equivalent to 2SLS estimation. Thus, we are relying on the standard IVassumptions for our instrument. Namely, we assume that conditional on predetermined observables, the instrument Post2002i · Under45i is independent of ui and vi. We justify this assumption on grounds similar to those of a DD analysis. That is, we assume that in the absence of our policy, the difference in leave patterns between those older and younger than the cohort turning 45 in 2002 would have remained constant. We assess the validity of this assumption using placebo regressions described below.
In order to test the key inequality in Equation 7 we first estimate the endogenous probit regression in Equation 10 via maximum likelihood estimation, with Li as the outcome and DCi, Post2002i, Under45i and Xi as regressors. These resulting parameters are then used to calculate βEndo with the sample analog of Equation 11. Next, we implement the 2SRI estimator. In the first stage, we first estimate the linear equation in Equation 12 and retain the residuals ^vi. In the second stage, we estimate Equation 13 by fitting a probit regression via maximum likelihood, with Li as the outcome and Post2002i, Under45i, Xi and ^vi as regressors. We then calculate βExog with the sample analog of Equation 14. Standard errors are adjusted for the fact that the regressor ^vi is estimated in the first stage regression.17
Our estimates provide proxies for the relationship between mobility and DC enrollment in the endogenous case (βEndo) and the exogenous case (βExog) laid out in Section II. The endogenous probit estimates that compare mobility rates among DC participants and DB participants are driven by both the incentive effect and the selection effect. These two forces can, in general, lead to an ambiguous relationship between mobility rates across the two types of plans because the selection effect could reinforce or counteract the incentive effect. By Equation 7, we can rule out both a negative selection effect and no selection effect if we can reject the null hypothesis that the endogenous probit estimate is less than or equal to the 2SRI estimate (that is, H0: βEndo ≤ βExog). Therefore, the key statistic for testing for positive selection is the p-value for this null hypothesis; we report this for each specification in our results tables.18
We test the robustness of our results and the plausibility of our identification assumption in several ways. First, we eliminate various years prior to the plan transition to demonstrate that our results are not driven by a particular pretransition year. Second, we perform a variety of falsification exercises where we either assume the plan transition occurred in a year prior to 2002 at the same age-45 threshold, or that the age threshold for the default assignment in 2002 was either lower or higher than age 45. Because there does not exist an analog to Equation 12 in these placebo exercises, we instead report the results of reduced-form regressions, which replace DCi in Equation 10 with Post2002i · Under45i. We also provide additional results using an alternative definition of our control group in the pretransition years in Appendix 3A. Specifically, we show that our results are not driven by differences in leave probabilities among very young and very old workers by limiting the sample to ages close to 45 in Appendix 3C. Finally, we consider an alternative approach to accounting for an endogenous regressor in the context of a nonlinear model, namely a Local Average Response Function (or LARF, Abadie 2003) in Appendix 4. We are reassured by the fact that our results are virtually identical when using this independent method of addressing endogeneity.
V. Results
In this section, we report the results of our test for positive selection based on Equation 7. We evaluate these main results for one-, two-, and three-year leave outcomes. We also report our estimates of the incentive effect—that is, the effect of DC enrollment on turnover after adjusting for selection. We then examine the robustness to dropping various preplan transition years from the analysis and provide an extensive analysis of placebo default assignments in different years or at different ages younger or older than age 45. Finally, we briefly discuss robustness to our definition of age, vesting status, other sample restrictions, and our method of addressing endogeneity.
A. The Selection Effect
We report our findings for the three measures of leave propensities. For each outcome, we start by reporting the inputs to the selection test, namely the average partial effect using the endogenous probit regression (Equation 11) in the first row, followed by the average partial effect using the exogenous 2SRI probit (Equation 14) in the second row. The third row provides the p-value of the test of the null hypothesis that βEndo ≤ βExog, which is the key inequality from Equation 7 for detecting positive selection. The results tables also include the mean leave probability prior to the default retirement plan change for each estimation sample and the F-statistic from the first stage regression. The three columns represent different combination of controls. The first column includes only controls for Under45i and Post2002i. The second column adds controls for gender, race, hours, base salary, tenure at the employer, and dummies for department. The third column mirrors the second column but replaces Under45i and Post2002i with age and year fixed effects.
We begin by estimating the effect of DC plan enrollment relative to DB enrollment on the probability of leaving the employer within the next calendar year and report the results in Table 2. The endogenous estimate of the correlation between DC plan enrollment and leaving the employer is negative but not significantly different from zero in all three specifications. By contrast, βExog is negative and statistically significant. Together, these two estimates imply a p-value for our hypothesis test for selection that consistently allows us to reject the null hypothesis that βEndo ≤ βExog at the 1 percent level. Thus, based on Equation 7, βSelection > 0 because βEndo – βExog is strictly positive. We therefore conclude that mobility tendencies are positively related to preferences for the DC plan relative to the DB plan (that is, the selection effect is positive). Our results show a strong and robust first-stage relationship, as evidenced by the first stage Fstatistics. Results from the first stage indicate that employees belowthe age-45 threshold are about 52 percentage points more likely to enroll in the DC plan than employees age 45 or older (not reported).
For two-year and three-year leave outcomes, we find a similar pattern of results. Tables 3 and 4 report estimates and the test for selection using the same format as Table 2, but use a dependent variable that measures whether the employee leaves the employer within two years or three years, respectively. For these analyses, the sample is substantially smaller than that used for the one-year time horizon in order to eliminate employees in the pretransition period whose two- or three-year horizons cross the 2002 introduction date of the DC plan. Results from the two-year leave outcome consistently produce a negative and significant βExog and strongly reject the null hypothesis from Equation 7 in favor of positive selection at the 1 percent significance level. We also reject the null hypothesis at the 1 percent significance level when using the three-year leave outcome; results are shown in Table 4.
B. The Incentive Effect
While our focus above has been on identifying the role of selection, the results for βExog provide estimates of the incentive effect, that is, the direct effect of the DC plan on mobility relative to the DB plan. The estimates in Table 2 indicate that the incentive effect is negative and sizable in magnitude: For Column 3, the direct effect of the DC plan on mobility relative to the DB plan is a 5.6 percentage point reduction in one-year turnover, a 73 percent reduction relative to the mean.
Our negative incentive effect is counter to conventional wisdom that, relative to DB plans,DC plans ought to increase mobility due to greater portability. Our results suggest an alternative perspective, namely, that other attributes of the benefit, such as individual control, liquidity, and transparency, may generally make this DC plan more attractive than theDBplan and increase the likelihood that one remains with the employer in a way that dominates portability. Furthermore, as mentioned above, the importance of portability is reduced in our context given that the DB plan is less backloaded than typical DB plans.19
Finding a negative incentive effect can be further corroborated with research that shows employees place a low value on additional DB benefits: Fitzpatrick (2015) finds that public teachers in Illinois would trade just $0.20 in current compensation for an additional dollar of DB benefit (measured in present discounted value terms). We perform a back-of-the-envelope calculation to determine the valuation of DC benefits relative to DB benefits needed to square the magnitude of our incentive effect with existing estimates of the elasticity of employee turnover with respect to a dollar of employee benefits. Assuming such a low valuation of a dollar of DB benefits ($0.20), employees in our sample would have to only value a dollar of DC benefits at $0.55 in order to generate the patterns we observe in our sample.20
C. Robustness Checks
In this section, we first evaluate the robustness of our results by examining the sensitivity to removing various pretransition years of data that serve as our control. Second, we perform falsification exercises in which we vary the year of the plan transition or the age threshold of the default assignment rule.
1. Robustness to removing control years
To assess whether a particular year of data from the control period is driving our results, we execute our estimation strategy using different combinations of pretransition years. For our one-year leave outcome, our baseline analysis uses pretransition data from 1999, 2000, and 2001, which implies that we can test the sensitivity of the estimates using five additional combinations of these data by eliminating one or two years of data at a time. We can repeat this for our two-year leave outcome, but can consider only two possible subsamples because our baseline analysis only uses 1999 and 2000 from the pretransition period. We cannot conduct this sensitively analysis for the three-year leave outcome because we only use one year of pretransition data in the baseline analysis.21
We report βEndo, βExog, and the p-value for our test of positive selection for the baseline analysis and these alternative subsamples in Table 5 for the one-year leave outcome and in Table 6 for the two-year leave outcome. For each of these tables, we report results from specifications using the full set of controls.
For the one-year leave outcome (Table 5), we reject the null hypothesis that βEndo ≤ βExog in favor of positive selection. All reported p-values are below the 5 percent significance level despite the reduced power. In addition, the βExog estimates in the various subsamples are similar to the baseline results. Results for the two-year outcome are shown in Table 6. We find consistent support for positive selection and a negative incentive effect for the two-year outcome, and the magnitudes of the negative incentive effects are in line with our main results.
Overall, these results indicate that our baseline empirical finding—that employees who choose DC plans over DB plans have higher underlying mobility tendencies—is not sensitive to the composition of the control group. In addition, the estimates showthat eliminating one pretransition year from the analysis results in qualitatively and quantitatively similar estimates for βExog.
2. Placebo plan transitions and default assignment rules
We do two sets of falsification exercises in order to check the plausibility of our identifying assumption that trends in unobservable determinants of mobility rates before and after the transition did not differ on either side of the age-45 threshold. First, we eliminate the plan transition year (2002) from our analysis and impose a placebo plan transition in 2000 to see if we find any evidence that employees on either side of the age- 45 threshold had differential mobility in 2000 relative to 1999. We also repeat this same exercise, but use 2001 as the placebo policy change year. Second, we assign a placebo age threshold that determines the default plan assignment and use data exclusively on one side of the original age-45 threshold to determine whether we find evidence of differential mobility rates on either side of the placebo age thresholds. Our identifying assumption implies that we should find no evidence of changes in our outcome variables in either the placebo plan transition years or at the placebo age thresholds.
Table 7 shows the results of our falsification exercises for all three leave outcomes. In Column 1, we report the reduced form results for one-year leave probabilities, where the coefficient represents the effect of being on the lower side of the assumed age threshold in the assumed transition year on one-year mobility.22 The top row reports the baseline reduced form results for comparison (that is, using the threshold of age 45 in 2002). The next two rows of results assume that the plan transition occurs in 2001 and 2000, respectively, with an age-45 threshold for the default plan assignment. Alternatively, Rows 4 and 5 use the original policy year, but change the age threshold. The “Age 32.5 Placebo” limits the sample to those younger than age 45, while the “Age 57.5 Placebo” limits the sample to employees age 45 and older.
Of these nine placebo tests, only one estimate—the three-year mobility rate for the lower age threshold—yields a coefficient that is significant at the 5 percent level. The remaining placebo coefficients in the table are statistically insignificant. Overall, the results from the falsification exercises provide support for the conclusion that our baseline findings on selection and incentive effects are likely to be a result of the retirement plan transition in 2002 that led to differences in retirement plan enrollment on either side of the age-45 threshold.
3. Sensitivity to alternative age definitions, vesting status, sample restrictions, and endogeneity correction
In our study thus far, our estimation procedure uses employees’ age as measured on September 1, 2002, the date of the plan transition. By assigning employees to either side of this age-45 threshold, we are able to evaluate the effect of the plan transition while controlling for any underlying differences between younger and older employees in this cohort. Alternatively, we could measure employee age in each calendar year and compare employees on either side of age 45 for that year. We report the results of plan enrollment on one-, two-, and three-year mobility rates using this alternative definition in Tables 3.2–3.4 in Appendix 3A. The results are consistent with our cohort analysis: the p-value of our test for selection is significant at conventional levels for all of the specifications. As for the incentive effects, the βExog estimates remain negative and statistically significant, although they tend to be slightly lower.
One may be concerned that the positive selection results are driven by employees who are vested in the DC plan but not vested in the DB plan due to differences in vesting requirements. When we restrict the analysis to employees vested in both plans (that is, at least five years of service), the positive selection effect remains, albeit weaker due to the reduced sample size (see Tables 3.5–3.7 in Appendix 3B). This finding suggests that the multidimensional difference between the two plans contributes to the positive relationship between mobility tendencies and preferences for the DC plan rather than differences in vesting alone.
We also explore the sensitivity of our results to alternative sample restrictions that exclude very young and very old workers for whomourmain identification assumption— that there are parallel time trends in the mobility of both age groups in the absence of the transition to the DC plan—may be more tenuous. In Appendix 3C, we show both DC enrollment and one-year mobility rates by year for a 5- and 10-year bandwidth on either side of age 45 in Figure 3.1. As shown in the figure, pretransition mobility rates among those over and under age 45 are much more similar when limiting the sample to those between the ages of 35 and 55 (10-year bandwidth) and even more so when the sample is limited to those between 40 and 50 (5-year bandwidth). However, in both samples, mobility rates decline for the Over 45 group relative to the Under 45 group in the post period.
These results are confirmed in the estimates presented in Table 3.8. The five-year bandwidth samples produce estimates of βExog that are similar in magnitude to those presented in Table 2 when the whole sample is used; the estimates using the 10-year bandwidth are slightly closer to zero. The βEndo estimates also are closer to zero for the restricted sample, and thus the difference between βExog and βEndo for each bandwidth is comparable to that estimated using the full sample. Due to the reduced power from the smaller sample size, our tests for selection fail to reject the null hypothesis at the 5 percent level when age and year fixed effects are included in the regressions. The results for assessing the null hypothesis also may differ due to attenuation of the βExog estimates. However, the results generally provide evidence that differences in mobility rates for very young and very old workers are not driving our main results.
Finally,we describe in Appendix 4 an alternative approach to addressing endogeneity in our nonlinear model—the Local Average Response Function (LARF) approach (Abadie 2003). We provide an overview of the method in Appendix 4A and report results in Appendix 4B. The results in Tables 4.9–4.11 are nearly identical to those of Tables 2–4. While the first row in the respective tables are by construction identical, the second rows rely on distinct approaches to accounting for endogeneity. In the case of 2SRI we rely on a control function approach, while in the case of LARF we use a reweighting procedure.23 Technically, the similarity between the results may suggest that the effect among the “complier” population is similar to the average treatment effect. This may not be too surprising, given the fact that our first stage regression implies that more than half of the population are among the “complier” group.
VI. Conclusion
The effect of a widespread transition in the employer-provided pension plan landscape from DB to DC plans on employee mobility has been a subject of interest among policymakers and academics because of the large number of firms and employees affected. Because DB pension wealth is typically tied more closely to tenure as compared to DC plans, conventional wisdom supports the idea that DC plans will induce higher mobility. However, this conclusion is complicated by the potential role of selection into employers and plan offerings by employees with differing underlying mobility tendencies. The effect of plan type on mobility is further confounded by the multidimensional difference between DB and DC plans, including features, such as individual control, liquidity, and transparency, that may make DC plans desirable enough to increase retention at firms with these plans.
In this paper,we exploit a natural experiment that created random variation in pension plan enrollment in order to study the effects of pension plan type on employee mobility. We develop an empirical model that helps us interpret the results from our analysis in the context of separate, and possibly countervailing, incentive and selection effects. This framework provides predictions regarding the different effects of endogenous and exogenous pension plan enrollment as they relate to the role of selection on unobservable mobility tendency. Our identification strategy relies on the assumption that the underlying difference in mobility tendencies between employees exogenously induced to remain in the DB plan (employees age 45 or older) employees who were exogenously induced to switch to theDC plan (employees younger than age 45) were the same before and after the employer’s plan transition in 2002. Our empirical results combined with insights from our model indicate that preferences for DC plans are positively related to unobservable mobility tendencies.
Although extrapolating from our single employer context to other settings may warrant caution, there are reasons to believe that our findings have some external validity. First, our theoretical framework allows us to intuitively consider how our results would vary in a setting with a more traditional, backloaded DB. Second, the employer in our study, a large university, features a diverse set of occupations covering a wide range of skill sets and responsibilities, making the results potentially applicable to a larger set of employers. At the same time, this employer offers more generous benefits relative to most private sector employers, which limits generalizability.
Our findings have a number of implications for mobility and the transition fromDBto DCplans. First, our results provide evidence of positive selection intoDCplans overDB plans based on mobility tendencies, implying that at least part of the relationship between the transition and increased job mobility is due to selection and not fully caused by differences in portability or accrual patterns across plan type. Taken directly, our finding implies that the selection effect is at least 3.6 percentage points, approximately half the one-year turnover rate in our setting. Comparing this to past findings that DC plans are associated with lower job tenure, on average, relative to DB plans (Munnell, Haverstick, and Sanzenbacher 2006), our results imply that the selection effect would fully explain this difference, although such a direct comparison warrants great caution.24
Second, because the transition we examine takes place within an employer among a set of covered workers, we can rule out the possibility that the differences in mobility we find are driven by compensating premiums, which have been used to explain a potentially large part of the mobility differences between covered and uncovered workers (Gustman and Steinmeier 1993). Third, we find evidence that, counter to conventional wisdom, DC plans may reduce mobility relative to DB plans. This suggests that one should not simply characterize the difference in plan features between DB and DC plans in terms of portability and accrual; rather, it is important to recognize that the differences are multidimensional, including differences in risk exposure, liquidity, and transparency, for example. Finally, we find that the incentive and selection effects work in opposite directions in our context. This finding combined with the multidimensional difference between the plans highlight the need for additional research to identify the role of rational and behavioral factors in the relationship between pension plan type and employee mobility.
Footnotes
↵1. Goda and Manchester (2013) document default effects in this same context using administrative data on plan enrollment from the year of the plan transition. This previous paper focuses on the effects of the default assignment on plan enrollment and the policy question of how to select the optimal age-based default rule given assumptions about employee risk preferences, financial market returns, and employee mobility. The present study evaluates the effect of plan type on subsequent mobility decisions using distinct data on employee turnover collected from before and after the plan transition and relies on the variation in plan enrollment resulting from the default rule in the estimation strategy.
↵2. Goda, Jones, and Manchester (2013) uses a technique that applies a regression discontinuity approach with data on mobility prior to the transition year and finds results qualitatively similar to but less precise than those presented here.
↵3. The model is similar in spirit to a Roy (1951) model where individuals self-select into a given state—for example, industry—based on the potentially heterogeneous returns to that state. In that case, the econometric recovery of the effect of said state on outcomes—for example, earnings—is obfuscated by the correlation between determinants of the outcome and selection into a given state. Such models have been applied in many contexts—for example, the study of selection into higher education (Willis and Rosen 1979) or selection into immigration (Borjas 1987). In our case, individuals may select into a type of retirement plan based on the value of that plan, and this potentially heterogeneous value subsequently affects the likelihood of staying with the firm.
↵4. In Appendix 1. A we recast our model using a potential outcomes framework, similar Imbens and Angrist (1994). Leaving is a function of benefit enrollment—Li = (Bi)—and benefit enrollment is in turn a function of the benefit regime—Bi = Bi(Z), for
. When the DB plan is the default, but employees may switch to a DC plan, Zi = 0; when all employees must enroll in the DB plan, Zi = 1; and when all employees must enroll in the DC plan, Zi = 2.
↵5. Continuing with the potential outcomes framework mentioned in footnote 4 and described in detail in Appendix 1. A:
↵6. Within the potential outcomes framework from footnote 4 and Appendix 1. A, we have:
↵7. This is because the distribution of ϕ among enrollees in the endogenous case is a center-truncated version of the distribution of ϕ among all employees under exogenous enrollment.
↵8. This may seem counterintuitive given the standard approach of signing omitted variable bias. However, the standard omitted variable bias intuition does not hold in the presence of heterogeneous treatment effects and selection on treatment.
↵9. In Section IV we outline our econometric methodology, Two-Stage Residual Inclusion, which allows us to account for endogenous benefit enrollment while accommodating a nonlinear specification. While the method technically implies that we recover an average treatment effect, one may be inclined to interpret our results as a local average treatment effect. In Appendix 1.D we discuss this alternative interpretation in more detail and show how it would alter our results.
↵10. This choice applied to union employees hired before January 1, 2001, and governed future benefit accruals only. All nonunion employees hired after this date were enrolled in the DC plan.
↵11. Nonunion employees were subject to an earlier plan transition on January 1, 1997. However, our data do not span this earlier policy change. Faculty and nonunion employees in supervisory roles were never offered benefits in a DB plan unless they experienced job changes that resulted in changes in employment group.
↵12. If the employee contributed 1, 2, 3, or 4 percent, the employer contributed 1.5, 3, 4, and 5 percent respectively.
↵13. Individuals with missing pension or demographic records were dropped from the analysis (12 individuals). Individuals who had DB accruals, but were rehired following the transition were also dropped (7 individuals).
↵14. See Goda, Jones, and Manchester (2013) for results using a fuzzy regression discontinuity.
↵15. We obtain qualitatively similar results using a linear probability model and 2SLS—we consistently reject our null hypothesis in favor of positive selection. However, we tend to estimate incentive effects much larger in magnitude, most likely owing to the fact that our outcome variable is binary and has a relatively low baseline mean. Linear probability model results are available from the authors upon request.
↵16. There are two possible ways to define “over” and “under” groups based on the cutoff of age 45 on September 1, 2002: cohort (for example, age 44 on September 1, 2002), and age (for example, age 45 on September 1, 2002). Our base set of results are estimated using the cohort definition; however, our results are robust to defining Under45i based on age rather than cohort.
↵17. See, for example, Newey and McFadden (1994) for results on the asymptotic properties of two-step estimators.
↵18. Inference in this case is adjusted to take into account sample correlation between βEndo and βExog.
↵19. Note that our findings cannot be explained by inertia among employees affected by the default because employees on either side of the age-45 cutoff faced a default plan.
↵20. We use the methodology from Goda and Manchester (2013) to determine the average net present value of DB and DC benefits for employees in our data and a turnover elasticity estimate from Manchester (2012) inferred from the retention response to a different form of employee compensation at this same institution, tuition reimbursement benefits. We then scale the value of a dollar of DC benefits relative to a dollar of DB benefits until we match our incentive effect on turnover.
↵21. Note that all of the alternative subsamples use the year 2002 because all posttransition outcomes are measured relative to that year in the baseline analysis.
↵22. For each of these falsification exercises, we report the reduced form results because a first stage is not possible for the falsification specifications.
↵23. In the case of a linear probability model, both approaches are equivalent to 2SLS. However, in the context of a nonlinear model, the difference between these approaches is nontrivial.
↵24. Munnell, Haverstick, and Sanzenbacher (2006) find that employees in a DB-only (DC-only) plan have 4.0 (2.7) years more tenure, on average, relative to a baseline average job tenure of 8.4 years. If a constant hazard rate is assumed, the implied difference in hazard rates between DC and DB plans would be approximately one percentage point.
- Received March 2015.
- Accepted March 2016.