Estimating the causal effect of Disability Insurance (DI) receipt on any outcome requires exogenous variation in who receives benefits, because DI receipt is strongly selected: recipients are sicker, less educated, and lower-earning than the general population, which confounds simple comparisons. Ordinary least squares (OLS) estimates are biased in both directions simultaneously — health selection biases them toward larger apparent disincentives; strategic application behavior biases them toward smaller ones. The empirical literature has developed four distinct identification strategies that exploit different sources of quasi-random variation to bypass this problem.
Two offsetting biases affect OLS estimates of DI's effect on labor supply:
At the initial Disability Determination Services (DDS) stage, health selection dominates — OLS understates the true local average treatment effect (LATE) (Maestas, Mullen, and Strand 2013). At the Administrative Law Judge (ALJ) appeal stage, the two biases approximately cancel — OLS ≈ instrumental variable (IV) (French and Song 2014). The net direction of OLS bias is therefore stage-dependent and cannot be assumed in advance.
Chen and van der Klaauw (2008) — Bound Update + Vocational Grid RD
Relationship to the rest of the literature: Chen and van der Klaauw occupy the methodological bridge between Bound's comparison-group approach (1989) and the quasi-random assignment strategies of MMS (2013) and French/Song (2014). The vocational grid RD is a direct precursor to the examiner/judge IV designs — both exploit the fact that conditional on applicant characteristics, a feature of the DI administrative process generates variation in award probability that is as-good-as-random near the margin.
Von Wachter, Song, and Manchester (2011) — Non-Applicant Extension:
Using 1981–1999 SSA application records linked to W-2 earnings (1978–2006), von Wachter et al. extend and update the comparison-group approach in two ways. First, they add matched non-applicants as a third benchmark, showing that rejected applicants earn 35,000 for non-applicants — far below what the non-applicant benchmark would be needed to support. The rejected group is not a valid stand-alone counterfactual for "what allowed beneficiaries would earn if denied" because it is severely impaired relative to the actual labor force. Second, they document that the composition of rejected applicants has shifted toward younger, lower-mortality, more marginally-impaired applicants over time (1982 → 1997 cohorts), raising the Bound upper bound across cohorts. The hearings-allowed subgroup — the complier population of French and Song (2014) — earns more (3,000 DDS-allowed) and works more (~24.5% vs. ~17.9%), consistent with the high-severity-end / low-disincentive ordering in MMS (2013). See Von Wachter Song and Manchester 2011 — Trends in Employment and Earnings of Allowed and Rejected Applicants to the Social Security Disability Insurance Program.
The most influential strategy exploits the fact that DI cases are assigned to examiners (at the DDS initial determination stage) or ALJs (at the appeal stage) in a rotation that is effectively random conditional on office and date. Examiners and judges vary substantially in their allowance rates despite receiving similar caseloads. This variation generates quasi-random assignment to benefit receipt.
Maestas, Mullen, and Strand (2013) — Initial DDS Stage
French and Song (2014) — ALJ Appeal Stage
Autor, Maestas, Mullen, and Strand (2015) — Processing Time as a Separate Channel
Maestas and Song (2011) — Program Exit Margin (DI-to-OA Conversion)
Convergence and revision: MMS (−28 pp) and French/Song (−26 pp) are remarkably close despite different identification strategies, different stages, different time periods, and different complier populations. However, AMMMS (2015) corrects the MMS single-IV estimate upward to −48 pp (year 3) using a joint two-IV system that disentangles the processing time channel from the receipt channel. The convergence of MMS and French/Song may partly reflect that both single-IV approaches underestimate the true receipt effect by a similar degree; whether the French/Song ALJ-stage estimate is subject to analogous processing-time bias is not yet established.
Black, French, McCauley, and Song (2024) — ALJ Stage, Mortality Outcome
See Bernard Black, Eric French, Jae Song, and Marginal Treatment Effect.
Gelber, Moore, and Strand (2016) — Income Effect on Earnings
Gelber, Moore, and Strand (2017) — Income Effect on Mortality
Implication for the work-disincentive literature: Because the RKD finds no labor supply effect at the bend points, the work disincentive documented by MMS and French/Song is a substitution effect — DI receipt as an outside option that reduces the attractiveness of work — not an income effect reducing work via wealth. The two effects operate on different margins and are identified by different designs.
Moore (2015) — DA&A Termination
Hemmeter and Bailey (2016) — FMR Exit Margin (Comparison Group / Upper Bound)
See Jeffrey Hemmeter and Michelle Stegman Bailey.
Autor and Duggan (2003) — Bartik Instrument
Autor and Duggan (2007) — Agent Orange Natural Experiment
Policy implication: Congress and SSA have exclusively targeted the substitution effect (Ticket to Work [TTW], trial work periods, Medicare continuation eligibility). The TTW program issued 12.2 million tickets but achieved successful workforce integration for fewer than 1,400 (0.01%). If income effects are comparably large, these programs address the wrong channel and will have near-zero leverage on aggregate DI labor force exit.
Deshpande, Gross, and Su (2021) use the same vocational grid RD as Chen and van der Klaauw (2008) — age cutoffs at 50 and 55 for Stage 5 applicants — but apply it to a new outcome domain: bankruptcy, foreclosure, home sales, and home purchases. This is the same complier population (Stage 5 vocational applicants near an age cutoff) generating estimates on the benefit side of the ledger rather than the cost side. Key causal estimates within 3 years: −31% bankruptcy (−0.77 pp), −34% foreclosure (−1.75 pp), −15% net home sale (−1.75 pp), +14% home purchase (+0.60 pp). No significant eviction effect. The paper also introduces the "office classification" strategy, exploiting heterogeneity across ~130 DDS offices in implementing the borderline age rule, as a robustness refinement to the standard RD.
The treatment is primarily a timing instrument: on average, those above the cutoff receive disability benefits for 0.9 additional months. The financial distress findings are conservative lower bounds on the full welfare gain from permanent receipt. See Nonhealth Risk and DI Insurance Value for how these estimates connect to the welfare decomposition in Deshpande-Lockwood (2022).
Deshpande and Lockwood (2022) ask a different question from MMS and French/Song: not "how much does DI receipt reduce labor supply?" but "does the resulting transfer produce enough insurance value to justify the efficiency cost?" Their sufficient-statistics framework finds that DI generates $8,700 in surplus per recipient (64% above a cost-equivalent tax cut), with 63% of that value coming from insurance against nonhealth financial risks rather than health-severity targeting.
The connection to the causal effects literature is direct: MMS and French/Song document a ~28 pp LFP reduction for marginal recipients, implying a substantial work disincentive. Deshpande and Lockwood's counterfactual earnings estimates show that marginal recipients' foregone earnings are only 10,000–15,000/year in cash transfers. The paper thus completes the cost-benefit accounting that the causal effects literature leaves open. See Nonhealth Risk and DI Insurance Value.
Deshpande and Mueller-Smith (2022) use the same Personal Responsibility and Work Opportunity Reconciliation Act (PRWORA) 1996 birthdate RD as Deshpande (2016b) but extend it to criminal justice outcomes via Criminal Justice Administrative Records System (CJARS) linkage. This study is conceptually distinct from the labor supply literature above: instead of asking how DI/SSI receipt affects work, it asks how SSI removal affects crime — a different margin, a different outcome domain, and a different complier population (youth at the age-18 redetermination threshold rather than applicants at the award stage).
Key estimates (IV = RD / 0.36, N=21,768 charge outcomes; N=26,991 incarceration):
The exclusive concentration in income-generating crimes (theft, burglary, fraud/forgery, robbery, drug distribution, prostitution) establishes income substitution as the mechanism, ruling out idleness or substance use. The crime response is an absorbing state: criminal records and incarceration foreclose legal employment progressively, so crime effects grow even as the direct SSI income gap narrows over the 16-year follow-up.
Cost-benefit: Marginal Value of Public Funds (MVPF) = 5.6 (without victim costs), 16.1 (with victim costs), versus Deshpande (2016b)'s MVPF of 0.90–1.03 for income and earnings outcomes alone. The crime channel is what makes SSI welfare-positive relative to most other social programs.
Chen (2012) uses the same SIPP-SSA linked data and accepted-vs.-rejected-applicant comparison framework as Chen and van der Klaauw (2008), but shifts the outcome from the applicant's own labor supply to the spouse's labor supply. The design is a fixed-effects event study (Jacobson-LaLonde-Sullivan) comparing wives of accepted DI applicants to wives of rejected applicants; both groups have disabled husbands, so post-award divergence in wives' labor supply isolates the crowd-out of DI income on the predicted Added Worker Effect (AWE).
Key estimates (N = 39,519 wives; 1980–2008):
This work is conceptually distinct from the recipient-level disincentive literature above: the estimand is how DI income changes household labor supply, not just the beneficiary's own work. The household-level analysis reveals an underappreciated insurance dimension: DI insures spouses against involuntary labor market entry, not just beneficiaries against income loss. See Added Worker Effect and Nonhealth Risk and DI Insurance Value.
Autor, Kostøl, and Mogstad (2015) use the same Norwegian judge-lottery IV design as French and Song (2014) but extend the analysis to the full household — tracing how DI denial ripples through own earnings, benefit substitution from other programs, and the spousal Added Worker Effect — and then imputing consumption from administrative registers to recover the program's consumption-insurance value by marital status. This is the first causal identification of the DI-specific AWE and the first household-level welfare analysis of DI using quasi-random assignment.
Design and setting: 75 ALJ-stage appeal judges randomly assigned within department×year cells, Norwegian National Insurance program, 1994–2005; N=14,077 appellants; consumption imputed from income-wealth registers using a budget-identity method.
Household income decomposition: The gross DI income shock is attenuated through four channels:
Marital status heterogeneity:
Willingness to pay:
Reapplication + spousal AWE together offset ~60% of the welfare loss from denial, confirming that DI functions primarily as consumption insurance for households without internal risk-sharing mechanisms.
See Added Worker Effect, Nonhealth Risk and DI Insurance Value, and Andreas Ravndal Kostøl.
Deshpande and Li (2019) use 118 SSA field office closings as an IV for application costs. This design identifies the effect of access on program participation, not the effect of receipt on labor supply or mortality — a distinct estimand from MMS, French/Song, Gelber/Moore/Strand, and Moore. The result (applications −10%, recipients −16%, so targeting worsens) is relevant to the causal effects literature because it characterizes the selection process that determines who enters the applicant pool at all: the marginal deterred applicant is approved-quality, not denied-quality, which means the LATE estimated by examiner/judge IV applies to a population that is systematically less impaired than the true eligible-but-deterred population. See DI Application Costs and Take-Up.
Staubli (2011) uses Austria's 1996 reform raising the relaxed-eligibility age from 55 → 57 for men as a difference-in-differences (DiD) instrument. The estimand differs from the US literature: this identifies the causal effect of eligibility criteria stringency on enrollment and labor market participation, rather than the causal effect of DI receipt on individual outcomes. It is included here as international comparative evidence.
Main results (treated = men 55–56; comparison = men 49–54; N=236,218 Austrian Social Security Database (ASSD) records):
| Outcome | DiD estimate |
|---|---|
| DI enrollment | −6.0 to −7.4 pp (base: 22.6%) |
| Employment | +1.6 to +3.4 pp |
| Unemployment | +3.5 to +3.9 pp |
| Total LFP (incl. UI/SI) | +6.1 to +7.5 pp |
Blue-collar workers show the largest employment response (+2.7 to +6.0 pp); white-collar workers show no employment effect — consistent with blue-collar workers being disproportionately at the eligibility cliff (pre-reform DI base 33.3% vs. 7.5% white-collar). The Austrian employment gain exceeds both Swedish (Karlström et al. 2008: no employment effect) and US (Chen and van der Klaauw 2008: moderate) estimates from similar reforms, attributed to Austria's reform targeting a younger, more employable margin.
The large spillovers to Unemployment Insurance (UI) and sickness insurance (together absorbing most of the DI reduction) are an important qualification: eligibility reform redistributes caseload across social insurance programs as much as it induces work. See Stefan Staubli, Vocational Grid, and Conditional DI Applicants.
Börsch-Supan and Jürges (2012) — German Five-Phase Reform History
Börsch-Supan and Jürges use Germany's pension reform chronology (1957–2008) as a sequence of before-after cohort comparisons, exploiting the fact that reforms took effect sharply by birth cohort. Three key reforms illustrate the institutional-incentive mechanism:
Because German mortality declined smoothly and monotonically throughout, the sharp reform-date discontinuities cannot be explained by health changes. The paper's verdict: "disability insurance appears to be mostly a train on its own track." Conditional on health level (mortality risk), LFP dropped dramatically as institutional exit options expanded: a man with 1% annual mortality risk had 91% LFP probability in 1970 but only 57% in 2000.
Unlike Staubli (2011) who uses formal DiD, and unlike the US examiner/judge IV studies, these are graphical before-after cohort comparisons without formal standard errors. The identification argument rests on the smoothness of the counterfactual health trend. See DI Uptake and Health Decoupling, Axel Börsch-Supan, and Hendrik Jürges.
The identification strategies above all focus on the work-disincentive side of the DI ledger — how receipt reduces labor supply. Low and Pistaferri (2020) supply the complementary accounting: what fraction of the genuinely disabled are not receiving benefits, and how does this reframe the labor supply estimates?
Type I and type II error rates:
Type I errors dominate type II errors in both frequency and welfare cost, reversing the standard narrative that DI is "too generous." The US system is calibrated toward reducing type II errors (strict standards, elaborate sequential process) at the cost of large type I errors.
Implications for interpreting labor supply estimates:
The MMS (2013) and French/Song (2014) estimates (−26 to −28 pp LFP reduction) are conditional on complier populations — those on the margin of program entry. The marginal denied applicant is in moderate health and has limited realistic employment alternatives. When the counterfactual LFP of denied applicants is taken into account (low baseline, typically 20–30% for the marginal DDS-stage applicant), the mechanical labor supply gain from denial is 12–17 pp — substantially below the raw LFP estimate. The difference between the raw 26–28 pp and the 12–17 pp mechanical gain represents applicants who would have had low labor force attachment whether or not they received benefits.
This does not overturn the causal estimates — MMS and French/Song correctly identify the LATE. It does affect welfare calculations: the insurance value of covering a type I error victim (a severely disabled person denied benefits) is high, and the labor supply cost of doing so is lower than face-value estimates suggest.
The five-dimensional design space: Low and Pistaferri (2020) organize DI policy reform along five axes, each affecting the type I/II error balance differently:
See Low and Pistaferri 2020 — Disability Insurance Theoretical Trade-Offs and Empirical Evidence.
Design: Health and Retirement Study (HRS) wave 4 (ages 50–64, N=7,960) linked to SSA administrative records (MBR, SSR, MEF). Four pairwise propensity-score comparisons: DI/SSI beneficiaries with mental illness diagnosis vs. (a) never-applied non-beneficiaries with evidence of mental illness and (b) rejected/uncertain applicants with evidence of mental illness; same comparisons for physical-diagnosis beneficiaries. This is not an IV design — it measures differences conditional on observable health and demographic characteristics, not causal effects of DI receipt.
Key findings:
After propensity score reweighting, approved and rejected DI/SSI applicants with mental illness are economically indistinguishable:
Health insurance is the sharpest benefit: 90.5% of mental illness DI beneficiaries are insured vs. 53.1% of rejected/uncertain applicants (p<0.001), a gap that persists after reweighting (49.8% reweighted, p<0.001).
Mental illness DI beneficiaries are worse off than physical-disability DI beneficiaries on every dimension: household income (28,824), own earnings (6.6% any vs. 18.9%), marriage rate (42.1% vs. 65.2%), net non-housing wealth (77,253).
Interpretation: The income/wealth parity between approved and rejected mental illness applicants is consistent with the program accurately screening on unobservable dimensions of need. It also implies that denial does not lead to meaningful earnings recovery — rejected applicants with mental illness have near-zero own earnings ($0 median), leaving denial to eliminate benefits without offsetting earned income. Health insurance, provided via Medicare (DI) or Medicaid (SSI), is the clearest welfare gain with no confounding selection interpretation.
The "marginal applicant" framing — that mental illness applicants are relatively healthy and gaming the system — is directly contradicted: rejected mental illness applicants are worse off than rejected physical-impairment applicants on nearly every measure.
See John Bound, Kyle Caswell, Timothy Waidmann, and DI Denied Population.
Bound, Lindner, and Waidmann (2014) address a tension that runs through the entire causal effects literature: aggregate time-series studies attributed most of the post-1980 employment decline among work-limited men to DI expansion, while IV and comparison-group studies found smaller point estimates (15–30 pp). The paper resolves this not by estimating a new causal effect but by decomposing employment changes using SIPP matched to SSA administrative records at three snapshots: 1990, 1996, and 2004.
Three-bin decomposition: The work-limited male population is split into (1) DI/SSI beneficiaries, (2) denied applicants, and (3) non-applicants with work limitations. Tracking each bin's size and employment rate across snapshots separates the contribution of program expansion from other forces.
Key findings:
Reconciliation: Aggregate studies overstate DI's causal role by treating the co-occurrence of DI expansion and employment decline as attribution. The IV estimates — Bound (1989) ~30 pp upper bound, French and Song (2014) ~26–28 pp ALJ judge-IV, von Wachter et al. (2011) 15–30 pp — are internally consistent with each other and with the decomposition. The disjoint periods (growing DI + declining employment in the early 1990s; flat DI + declining employment in the late 1990s) confirm that the IV causal estimates identify a genuine but partial-equilibrium effect that does not account for the full secular trend.
Policy implication: DI is not the primary driver of the long-run decline in employment among men with work limitations. Policies aimed at reversing that decline via DI reform will address at most a fraction of the phenomenon.
See John Bound, Stephan Lindner, Timothy Waidmann, Eric French, Jae Song, and Till von Wachter.
| Study | Strategy | Outcome | Estimate | Complier / Scope |
|---|---|---|---|---|
| Chen & van der Klaauw 2008 | Comparison group (Bound update) | LFP (upper bound) | −14 to −21 pp (raw to bias-adj.) | All 1990s SIPP applicants; smaller than Bound's 30 pp |
| Chen & van der Klaauw 2008 | Fuzzy RD (vocational grid age cutoffs) | LFP | ~−11 to −16 pp | Stage 5 vocational applicants near age cutoff |
| Deshpande, Gross & Su 2021 | Fuzzy RD + office classification (grid cutoffs) | Bankruptcy (3 yr) | −0.77 pp (−31%) | Stage 5 vocational applicants near age cutoff |
| Deshpande, Gross & Su 2021 | Fuzzy RD + office classification (grid cutoffs) | Foreclosure (3 yr, homeowners) | −1.75 pp (−34%) | Stage 5 vocational applicants near age cutoff |
| Deshpande, Gross & Su 2021 | Fuzzy RD + office classification (grid cutoffs) | Net home sale (3 yr) | −1.75 pp (−15%) | Stage 5 vocational applicants near age cutoff |
| Deshpande, Gross & Su 2021 | Fuzzy RD + office classification (grid cutoffs) | Net home purchase (3 yr) | +0.60 pp (+14%) | Stage 5 vocational applicants near age cutoff |
| Maestas & Song 2011 | Program exit margin RD (FRA DI-to-OA conversion) | Annual earnings (intensive margin, recent-work-activity) | ~+63% recovery at age 67 vs. age 66 trough | ~12% of DI beneficiaries with recent LFP; lower bound on full population |
| Maestas & Song 2011 | Program exit margin RD | LFP > SGA (recent-work-activity early entrants) | −24% at age 64 → −15% at age 66 → +25% at age 67 | Same subsample; lower bound |
| MMS 2013 | DDS examiner IV (EXALLOW only) | LFP, 2 yr | −28 pp (biased; see AMMMS 2015) | Marginal ~23% at initial determination |
| AMMMS 2015 | DDS examiner IV (EXTIME) | Employment per month processing delay | −0.52 pp/month (yr 3) | All 2005 SSDI applicants, DDS stage |
| AMMMS 2015 | DDS joint IV (EXALLOW + EXTIME) | LFP, 3 yr (corrected receipt) | −48 pp | All 2005 SSDI applicants, DDS stage |
| French & Song 2014 | ALJ judge IV | LFP, 3 yr | −26 pp | ALJ appellants |
| French & Song 2014 | ALJ judge IV | Annual earnings, 3 yr | −$4,059 | ALJ appellants |
| Gelber et al. 2016 | RKD (benefit amount) | Annual earnings | −1 DI | Upper bend point (84th pctile AIME) |
| Gelber et al. 2017 | RKD (benefit amount) | Annual mortality | −0.26 pp per $1k | Lower bend point (4th pctile AIME) |
| Gelber et al. 2017 | RKD | Cost per life-year | $58,574 | Lower bend point |
| Moore 2015 | DA&A termination | Employment >SGA | +22 pp (peak) | DA&A subgroup, 2.7-yr duration peak |
| Hemmeter & Bailey 2016 | Comparison group / upper bound (FMR exit margin) | Earnings >SGA/poverty (upper bound) | +43 pp | FMR-selected DI workers 1998–2008; non-random, pre-selected for medical improvement |
| Autor & Duggan 2003 | Bartik IV | Labor force exit | ×2 for dropouts | Aggregate; low-skill displaced workers |
| Autor & Duggan 2007 | VDC DiD (non-work-contingent) | NILF (pure income effect) | +3.21 pp | Vietnam-era vets, near-elderly; preliminary |
| Deshpande & Mueller-Smith 2022 | Birthdate RD / PRWORA (SSI removal) | Income-generating charges | +0.380 IV (control mean 0.625) | SSI youth at age-18 redetermination |
| Deshpande & Mueller-Smith 2022 | Birthdate RD / PRWORA (SSI removal) | Annual incarceration likelihood | +2.9 pp IV (control mean 4.7%) | SSI youth at age-18 redetermination |
| Autor, Kostøl & Mogstad 2015 | Norwegian judge-lottery IV | Consumption change (denial → allow) | Married: −9,835* | ALJ-stage appellants, Norway 1994–2005 |
| Autor, Kostøl & Mogstad 2015 | Norwegian judge-lottery IV | Spousal AWE (earnings, year 1) | +$6,000 spouse earnings when denied | ALJ-stage appellants, Norway 1994–2005 |
| Autor, Kostøl & Mogstad 2015 | Norwegian judge-lottery IV | WTP for DI (static) | Married ~9,100 per capita | ALJ-stage appellants, Norway 1994–2005 |
| Black et al. 2024 | ALJ judge IV | 10-yr mortality | +2.8 pp LATE (marginal); negative for inframarginal | ALJ appellants 55–64, 1995–2004 |
| Bound, Lindner & Waidmann 2014 | Decomposition (SIPP-SSA, 3 bins × 3 years) | Share of employment decline attributable to DI | 50–100% (1990–96, extreme assumptions); 20–50% (1996–2004) | Work-limited men; diagnostic, not causal |
The near-identical estimates from two designs targeting different stages and populations provides strong evidence of external validity. The complier at the DDS stage (those on the margin of initial allowance, concentrated in mental disorders) and the complier at the ALJ stage (those who appealed an initial denial) are different populations — yet both show ~26–28 pp LFP reductions. This implies the causal work-disincentive is not specific to a narrow margin population.
At the initial DDS stage (MMS), OLS understates the LATE — health selection (sicker people more likely allowed) dominates, making the estimated disincentive look smaller than the true causal effect on compliers. At the ALJ stage (French/Song), OLS ≈ IV — the health and work-propensity selection biases cancel for this more selected applicant pool. Neither result generalizes to non-applicant populations.
Three converging pieces of evidence all point to income effects — not substitution effects — as the dominant channel through which DI reduces labor supply.
Autor and Duggan (2007) — conceptual framing and VDC evidence: The paper distinguishes the two channels and provides preliminary evidence from VDC, a non-work-contingent program: a 3.21 pp NILF increase among Vietnam veterans after an unearned income shock with zero substitution effect. This was the first attempt to isolate the pure income effect in a disability transfer context.
Gelber, Moore, and Strand (2016) — RKD on benefit amount: Directly isolates the income effect of DI payment size using the upper bend point kink: 0.20 decrease in annual earnings. This 20-cent estimate is nearly identical to the total crowdout found by MMS (2013) (18–19 cents) and French/Song (2014) (19 cents). The implication: the SGA substitution effect — the large notch in the budget constraint that penalizes earnings above ~$1,000/month — contributes almost nothing to the observed work disincentive. The income effect alone is sufficient to explain the observed reduction in earnings.
Ticket to Work failure: Fewer than 1,400 of 12.2 million tickets led to workforce integration (0.01%). Ticket to Work eliminates the substitution disincentive (explicit SGA waiver, Medicare continuation). If the TTW success rate were substantially above zero, it would constitute evidence that the substitution channel matters. The near-zero success rate is consistent with AD (2007): beneficiaries' preference for early retirement is driven by income, not the implicit tax.
This matters for welfare analysis: income effects are not conventionally distortionary (they don't create excess burden through labor market misallocation), whereas substitution effects do. A program whose work disincentive is driven by income effects is less distortionary than one driven by SGA avoidance — and this body of evidence suggests DI's disincentive is closer to the former.
Gelber/Moore/Strand (2017) add a further dimension from the lower bend point: mortality falls with income, but with no earnings response. Together the two companion papers span the income distribution: at the bottom (lower bend point), DI income buys necessities that extend life; higher up (upper bend point), it reduces labor supply via income effects on leisure. Neither effect operates primarily through SGA substitution.
Across MMS (2013) and French/Song (2014), the same groups show smaller work-disincentive effects: older workers (near Social Security retirement age), college graduates, and those with mental illness. The same groups show larger effects: younger workers, those with physical injuries (musculoskeletal, trauma). This convergence is strong evidence that the heterogeneity reflects genuine differences in residual work capacity rather than instrument-specific artifacts.
French and Song document that >60% of ALJ-denied applicants eventually receive benefits within 10 years. This means the question "what is the work-disincentive of DI receipt?" partly conflates two populations: those permanently excluded (the ~40%) and those eventually allowed (the ~60% who hold down earnings below SGA during appeals). A strict denial policy is therefore primarily a delay mechanism for most applicants, not an exclusion mechanism — with the attendant costs of earnings suppression, health deterioration during waiting, and administrative burden.