### 3.1 Exploiting variations in the timing of incarceration

In our benchmark model, we follow LaLonde and Cho (2008) in comparing the post-prison records of released prisoners to the pre-prison records of similar prisoners incarcerated later. The estimated model is a random-effects panel regression,

$$ {y}_{it}=\alpha {X}_{it}+\delta {Z}_i+{\displaystyle \sum_{q=-4}^{28}}{\beta}_q{Q}_q+{\displaystyle \sum_{t=2}^{84}}{\gamma}_t{T}_t+{u}_{it}, $$

(1)

where *y*
_{
it
} stands for the outcome variable (days in work, daily earnings) for person *i* in month *t*, *X*
_{it} and *Z*
_{i} are time-variant and time-invariant covariates, *T*
_{
t
} is a dummy variable equal to 1 in month *t* and 0 otherwise, while *u*
_{
it
} is a residual term. The *Q*
_{
q
} dummies denote relative time–set to 1 if person *i* is *q* quarters away from any quarters spent in prison, either partly or entirely. Thus for any quarter containing time in prison, *q* is set to 0. *Q*
_{
0
} = 1 covers the quarters of incarceration, prison and release; *Q*
_{
1
} = 1 stands for the first full quarter after release; and so on.

The *β*
_{
q
} coefficients measure the effect of relative time on the outcome variable, conditional on the *X* and *Z* characteristics and keeping calendar time constant. The reference period is all quarters preceding the quarter of imprisonment by more than a year. A coefficient of *β*
_{
6
} = −0.1, for instance, would suggest that the outcome variable is estimated to be 10 percentage points lower for those in their sixth full quarter after release than for offenders more than one year before their incarceration.^{Footnote 5}

Several caveats apply to the overlapping cohorts model of equation (1).

First, the strong correlation between calendar time and relative time means there is a risk of invalid results about individual predictors, including relative time effects. This is particularly the case on the margins of the observation window: the 25th post-prison quarter, for instance, can only occur in 2008, and the same problem arises when a pre-prison quarter substantially precedes the date of incarceration. In order to reduce the risks arising from multicollinearity, one should either widen the brackets of relative time or narrow the time window to a range where there is sufficient variation of calendar time at a given level of relative time. Our experiments suggest that this range is located at |q| < 11, where the correlation between calendar months and relative quarters is 0.32, as opposed to 0.63 in the whole sample, and 0.91 if |q| ≥ 11.^{Footnote 6} To check whether multicollinearity is a problem, we repeat the estimation after narrowing the time window to 10 quarters before and after time in prison.

Second, this specification cannot deal with offenders who served several prison sentences in the period observed. Recidivists *q* quarters after a prison spell can also be *q* + *x* quarters after another prison spell, and several quarters before their next spell, and so we cannot define a relative time variable for them in the way we do for non-recidivists. Therefore, we estimate equation (1) for offenders with a single prison spell and include recidivists in another model introduced in Section 4.4.

Third, it should be taken into consideration that the relative quarter dummies relate to populations of different size. We have plenty of observations at the level of *y*
_{
it
} one quarter before or after prison, but the data for the -27th or 27th quarters come exclusively from cohorts incarcerated in 2008 Q3 or released in 2002 Q2, respectively. Therefore, it is important to assess how the time path of the overall average (constructed from the means of *y*
_{
it
} across all cohorts observed in *t*) relates to the time paths followed by the individual cohorts.^{Footnote 7}

Last but not least, estimating a random-effects equation is tantamount to assuming that the residual is uncorrelated with unobserved individual attributes affecting the outcome. With only a few control variables to hand, the risk of such correlation is high, and there is a strong case for estimating fixed-effects models.

### 3.2 Fixed-effects estimates

Estimating equation (1) by simply allowing for individual fixed effects is infeasible, because calendar time and relative time are very strongly correlated within personal histories. (If we had relative month dummies instead of quarter dummies, the correlation would be perfect by construction for persons serving only one month in prison.) Therefore, we set fairly wide brackets for relative time: 1–8 quarters and more than eight quarters before/after the prison quarters. In equation (2), these periods are labelled ‘shortly before’, ‘long before’, ‘shortly after’ and ‘long after’. The residual *u*
_{
it
} is decomposed to an individual fixed effect (*c*
_{
i
}) and a residual term (*ε*
_{
it
}) assumed to be uncorrelated with the regressors.

$$ \begin{array}{l}{y}_{it}=\alpha {X}_{it}+\delta {Z}_i+{\beta}_1\cdot shortly\_{before}_{it}+{\beta}_2\cdot priso{n}_{it}+{\beta}_3\cdot shortly\_{after}_{it}+{\beta}_4\cdot long\_{after}_{it}\\ {}\kern2.76em +{\displaystyle \sum_{t=2}^7}{\gamma}_t{T}_t+{c}_i+{\varepsilon}_{it}\end{array} $$

(2)

The model compares post-prison outcomes to the same person’s pre-prison outcomes: a coefficient of *β*
_{
3
} = −0.1, for instance, would mean that the outcome variable is 10 percentage points lower in the first eight quarters after release than it was more than eight quarters prior to incarceration.

### 3.3 Taking care of unobserved recidivism

In the case of offenders incarcerated *before* the period of observation, ‘pre-prison’ employment and wages bear the effect of previous prison experience–and this leads to an underestimation of the negative consequences of incarceration (Holzer 2007). Due to a lack of information on the previous criminal records of offenders, one has to fall back on second-best solutions, such as starting the analysis later than the start date of the observed period, as LaLonde and Cho (2008) do. Therefore we repeat the fixed-effects estimations for offenders incarcerated in 2005–08. In choosing this sub-sample, we utilize the information available on recidivism: 80% of those who returned to prison within our seven-year window of observation did so within three years, and more than 95% returned within five years. Therefore, we can be confident that the great majority of those incarcerated in 2005–08 had not been in prison before 2002.

### 3.4 Estimates for recidivists

As discussed previously, we expect differences in the post-release behavior of one-time offenders and of recidivists. To assess how this difference affects labor market outcomes, we estimate equation (3).

$$ {y}_{it}=\alpha {X}_{it}+\delta {Z}_i+{\beta}_0\cdot priso{n}_{it}+{\beta}_1\cdot betwee{n}_{it}+{\beta}_2\cdot afte{r}_{it}+{\displaystyle \sum_{t=2}^{84}}{\gamma}_t{T}_t+{c}_i+{u}_{it} $$

(3)

The model is estimated separately for recidivists and for offenders with a single prison term in the period observed. In the equation, *prison* stands for the months in custody, *between* denotes months between two prison spells, and *after* indicates months after the last observed prison sentence. The reference category is the period before incarceration. The *between* dummy is obviously omitted for non-recidivists. The equations are estimated with fixed effects.^{Footnote 8}

We anticipate that the *β*
_{
2
} coefficients will be similar for the two groups under examination. For recidivists, the *β*
_{
1
} coefficients are expected to indicate a significant negative impact on employment and a weak effect on wages, as they capture the outcomes in a period when the stigma effect is present but the ‘reform effect’ is absent.