The Effect of Integration Policies in Denmark

Balance Tests and Sampling Design

Merlin Schaeffer (KU) & Teresa Freitas Monteiro (CERGE-EI)

2026-10-05

Danish refugee policies, 1950–2025

Policies are placed at the date they took effect.

Red = the five policies we study; grey = context. Point out that for language training and Start Aid the sampled cohorts straddle the reform date, and for permanent residency the cohorts arrived years before the 2007 reform but differ in whether they could finish the integration program before the cutoff (29 Nov 2006).

What the reference studies found

	Study	Refugees	Their children
Placement 1986–1998	Foged, Hasager & Peri (2024); Damm & Dustmann (2014)	A strong local labour market raises long-run employment and earnings; placement near co-nationals does not	More convicted youths in the assigned neighbourhood means more convictions later, among boys only
Placement 1999–2015	Azlor, Damm & Schultz-Nielsen (2020); Diop-Christensen et al. (2024)	A municipality with a 1 pp higher employment rate raises employment by .5–.6 pp after two to four years; the three-year residence requirement delays moving but does not prevent it	Not studied
Language training 1999	Foged, Hasager, Peri, Arendt & Bolvig (2024, 2023)	Permanent earnings gains, more schooling, more communication-intensive jobs	Higher lower-secondary completion and less juvenile crime, driven by boys below school age when the parents were trained
Welfare cut 2002	Dustmann, Landersø & Andersen (2024)	Employment up in the short run only; poverty and subsistence crime up	Lower language test scores, fewer years of schooling, teenage crime roughly doubled
Permanent residency 2002	Arendt, Dustmann & Ku (2025)	Employment of those affected fell and language proficiency barely moved: discouragement at the bottom	Not studied

Damm & Dustmann, AER 104(6), 1806–32. Foged, Hasager & Peri, JOLE 42(S1), S335–S377. Foged, Hasager, Peri, Arendt & Bolvig, ReStat 106(4), 1157–66, and Journal of Public Economics (2023). Dustmann, Landersø & Andersen, AEJ: Economic Policy 16(2), 406–41. Arendt, Dustmann & Ku, JOLE 43(2), 293–318. Azlor, Damm & Schultz-Nielsen, Labour Economics 63, 101808 (dispersal 1999–2010). Diop-Christensen, Diop & Munzula, JEMS 51(15), 3866–88. Every outcome here comes from registers — schooling, earnings, convictions. None of these studies observes what people think, feel or report about the policies.

Five policy regimes, and for three of them we already know something about the second generation — unusual, and part of why Denmark is the right case. The two without it are the ones at the ends of our period: the post-1999 quota placement and permanent residency. Two patterns worth holding on to. First, the children’s effects run in the same direction as the parents’: language training helped both, the benefit cut harmed both. Second, the evidence is not balanced across policies: for the 1999 placement regime the adult evidence is thinner than for 1986–1998, and for neither it nor permanent residency has anyone looked at the children. And what none of this literature has is survey data. Everything here is a register outcome: years of schooling, earnings, convictions. Nobody has asked these families what they experienced, which is the gap the sampling design at the end of the talk is meant to fill.

Identification strategies

Quasi-random placement

\[ \begin{aligned} y_{is} = {} & \beta_0 + \color{#901A1E}{\tau}\,\text{Z}_{mt} \\ & + X_i\beta_k + \text{cohort}_i + \varepsilon_{ism} \end{aligned} \]

\(Z\) municipality characteristics of municipality \(m\): first municipality (year \(t\)); \(X_i\): characteristics known at placement; \(s\): date of permission.

• Random allocation I: arrivals 1986–1998
• Random allocation II: arrivals Jul 1999 – Dec2015
• Assumption: given origin and family type, placement is random
• Balance test: individual characteristics do not predict municipality characteristics

Discontinuity in asylum date

\[ \begin{aligned} y_{is} = {} & \beta_0 + \color{#901A1E}{\tau} D_i \\ & + \beta_1 (a_i - c) \\ & + \beta_2 D_i \times (a_i - c)\\ & + X_i'\beta_3 + \varepsilon_{is} \end{aligned} \]

\(a_i\): asylum date; \(c\): cutoff; \(D_i = \mathbf{1}[a_i \ge c]\); triangular kernel, 548-day bandwidth.

• Language training: cutoff 1 Jan 1999
• Start Aid: cutoff 1 Jul 2002
• Assumption: refugees granted asylum just before and after the cutoff are comparable
• Balance test: no jump in predetermined characteristics at the cutoff

Difference-in-differences

\[ \begin{aligned} y_{i\tau} = {} & \alpha_i + \psi_\tau + \color{#901A1E}{\delta}\,\text{Post}_\tau \times T_i \\ & + X_{t(i\tau)}'\beta + u_{i\tau} \end{aligned} \]

\(\tau\): years since residency; \(T_i\): residency Jan–Oct 2004; \(\text{Post}_\tau = \mathbf{1}[\tau \ge 3]\).

• Permanent residency: residency Jan–Oct 2004 (treated) vs. Jan–Oct 2003 (control)
• Assumption: parallel trends without the reform
• Balance test: similar characteristics and outcomes in years 1–2

Designs follow Foged, Hasager & Peri (2024) and Arendt, Dustmann & Ku (2025).

Placement. Authorities placed refugees knowing only origin and family type, so conditional on those, where someone lands is as good as random. We regress outcomes on the characteristics of the first municipality (employment rate of non-Western immigrants, share of conationals) with individual controls and cohort fixed effects. Random allocation II applies the same logic to Jul–Dec arrivals 1999–2015.

Discontinuity. Both reforms applied to everyone granted asylum on or after a fixed date: 1 Jan 1999 (+430 hours of language training) and 1 Jul 2002 (benefits cut by about 40%). Local linear regression, triangular kernel, ±548 days bandwidth.

Difference-in-differences. The 2007 reform (2.5 years of employment plus intermediate Danish) hit everyone who had not finished the 3-year integration program by 29 Nov 2006. Residency by Oct 2003 could finish in time (control); residency in Jan–Oct 2004 could not (treated). Individual and years-since-residency fixed effects; post = year 3 onward.

Balance tests

Balance in reference studies

Foged, Hasager & Peri (2024), Table 4.

Arendt, Dustmann & Ku (2025), Table 1.

Welfare cut

	Foged, Hasager & Peri (2024)	Our data
	Welfare benefits (col. 1)	Replication	Our sample
Age 30–39 years	−.003 (.009)	.007 (.009)	.003 (.010)
Age 40–49 years	−.012 (.011)	−.002 (.011)	.001 (.012)
Age 50–55 years	−.020 (.017)	−.021 (.017)	−.033* (.019)
Female	.009 (.009)	.016* (.009)	.015 (.010)
Children 0–2 years	.003 (.011)	−.004 (.009)	−.005 (.010)
Children 3–5 years	.000 (.008)	−.007 (.008)	−.001 (.007)
Children 6–12 years	.008* (.005)	−.003 (.005)	.002 (.005)
Children 13–17 years	.008 (.006)	−.001 (.006)	.000 (.006)
Single	.002 (.012)	−.007 (.012)	−.004 (.012)
Africa	−.028 (.021)	−.027 (.021)	−.023 (.021)
Asia	−.061* (.034)	−.065* (.035)	−.078** (.039)
N	4,787	4,572	4,176
F	1.49	1.01	1.07
Pr > F	.13	.44	.38
F, adding Middle East	–	–	2.18
Pr > F	–	–	.01

OLS of a post-reform dummy on characteristics and asylum date, SEs clustered by date. Replication: Foged et al.’s code on our data. Our sample: aged 18–55 at entry, in Denmark in 2024, ±548 days. Reference: age 18–29, Middle East, Europe, and other regions. Timing: Foged et al. (2024) measure children and marital status in the first register year 1–5 years after the reform year, for refugees admitted before the reform partly after it; our sample measures them in the first register year after arrival. * p < .10, ** p < .05, *** p < .01.

The replication gets within 5% of their sample size and reproduces their coefficients closely (Asia −.065 vs. −.061, Africa −.029 vs. −.028); joint F = 1.01 (p = .44) vs. 1.49 (p = .13). In our sample the Foged et al. test also passes (F = 1.12, p = .34), but adding a Middle East dummy rejects balance (F = 2.22, p < .01): the origin mix shifts at the cutoff (Middle East share +.25), a dimension their test does not check.

Welfare cut: is the admission date manipulated?

	Window	Jump at the cutoff	Pr > |T|
Daily density test (rddensity)	±548 days	T = 1.31	.19
Monthly admissions, raw share	±12 months	+3.78 pp	.33
… net of seasonality	±12 months	+0.20 pp	.91
… net of seasonality	±24 months	+0.48 pp	.94
… net of seasonality, OLS	±24 months	+0.29 pp	.88

Refugees admitted 2000–2004, aged 18–55, excluding Afghanistan and Bosnia-Herzegovina, as in the balance test. The density test asks whether the daily number of permits jumps at 1 July 2002 (Cattaneo, Jansson & Ma). The monthly tests take each month’s share of its own year’s admissions and subtract what that calendar month usually is. The shaded band is the year around the cutoff, which is left out when the usual monthly pattern is computed; the red line is the reform date.

Nothing moves at the welfare cutoff. The daily density test passes (T = 1.31, p = .19) and so do the binomial tests in every window. Monthly admissions are noisier — the raw share of the year jumps by +3.8 pp against a monthly average of 8.3 — but nowhere near significant (p = .33), and net of the seasonal pattern it falls to a fifth of a percentage point. The OLS version is the most precise: it rules out shifts larger than about 4 pp, half a month’s worth of admissions. This is the cutoff where the design is least in doubt.

Language training

	Foged, Hasager & Peri (2024)	Our data
	Language training (col. 2)	Replication	Our sample
Age 30–39 years	−.010 (.009)	−.010 (.009)	−.006 (.009)
Age 40–49 years	.011 (.011)	.012 (.011)	.010 (.012)
Age 50–55 years	.005 (.018)	.010 (.018)	.030 (.022)
Female	.010 (.007)	.008 (.008)	.008 (.008)
Children 0–2 years	.004 (.011)	.016 (.011)	.009 (.011)
Children 3–5 years	−.009 (.009)	−.014* (.008)	−.013 (.008)
Children 6–12 years	.000 (.005)	.001 (.005)	.000 (.005)
Children 13–17 years	−.001 (.006)	−.002 (.005)	.001 (.006)
Single	.011 (.011)	.005 (.012)	.004 (.012)
Africa	−.032 (.027)	−.030 (.027)	−.025 (.028)
Asia	−.000 (.021)	−.004 (.023)	−.012 (.026)
N	5,188	5,018	4,680
F	.98	1.13	.88
Pr > F	.46	.34	.56
F, adding Middle East	–	–	1.58
Pr > F	–	–	.09

OLS of a post-reform dummy on characteristics and asylum date, SEs clustered by date. Replication: Foged et al.’s code on our data. Our sample: aged 18–55 at entry, in Denmark in 2024, ±548 days. Reference: age 18–29, Middle East and other regions. Timing: Foged et al. (2024) measure children and marital status in the first register year 1–5 years after the reform year, for refugees admitted before the reform partly after it; our sample measures them in the first register year after arrival. * p < .10, ** p < .05, *** p < .01.

Close replication: N = 5,038 vs. 5,188, F = 1.13 (p = .33) vs. .98 (p = .46), coefficients within about one standard error. Our sample: F = 1.00 (p = .44); with a Middle East dummy F = 1.70 (p = .06). The daily density test at the cutoff rejects, but permits always peak before the year end; the next slide tests monthly admissions net of that seasonal pattern.

Language training: is the admission date manipulated?

	Window	Jump at the cutoff	Pr > |T|
Daily density test (rddensity)	±548 days	T = −4.08	< .01
Monthly admissions, raw share	±12 months	−2.80 pp	.15
… net of seasonality	±12 months	+0.21 pp	.91
… net of seasonality	±24 months	−0.31 pp	.90
… net of seasonality, OLS	±24 months	−0.12 pp	.93

Refugees admitted 1997–2001 (the permit register starts in 1997), aged 18–49, excluding Somalia, as in Arendt et al. The daily test rejects because permits pile up before the turn of the year: the reform date is 1 January, so the seasonal pattern and the cutoff coincide by construction. The monthly tests remove that pattern. The shaded band is the year around the cutoff, which is left out when the usual monthly pattern is computed; the red line is the reform date.

Here the daily density test rejects sharply, T = −4.08 — though that number predates the imputed-permit-date correction and has not been re-run, and that is the result to explain rather than to report: 1 January is the one date where administrative seasonality has to produce a discontinuity, whatever refugees or caseworkers do. The same logic is behind the demeaned monthly-admissions test in the authors’ own replication code. The raw share of the year drops by 2.8 pp at the cutoff, a third of a month’s admissions, which is what the daily test is picking up. Net of the calendar pattern the jump is +0.24 pp at ±12 months, −0.30 at ±24 and −0.10 by OLS, none of them close to significant, with the OLS ruling out shifts beyond about 2.5 pp against a monthly average of 8.3. So the bunching belongs to the register, not to the refugees — and the language RD survives it.

Still in Denmark in 2024?

	Still here in 2024	Jump at the cutoff	Pr > |T|	Refugees
Welfare cut (1 Jul 2002)	.895	.041* (.023)	.08	4,608
Language training (1 Jan 1999)	.905	−.015 (.019)	.44	5,021

* p < .10, ** p < .05, *** p < .01.

Nine in ten refugees admitted around either cutoff are still in Denmark two decades later. At the language cutoff nothing moves. At the welfare cutoff there is a jump of 4.3 percentage points, p = .06 — and note the sign: refugees admitted after the benefit cut are more likely to still be here, not less, which is the opposite of what a return-migration story would predict. Marginal, but it matters for everything else in the talk: our sample is built from people present in 2024, so it conditions on an outcome that itself moves at the cutoff. That is the sampling-design problem in one line — a survey drawn from the people who are here today is a survey of stayers, and who stays is not independent of the reform.

Initial municipality placement

	Foged, Hasager & Peri (2024)	Our data
	Share of co-nationals (col. 4)	Replication	1986–1998	1999–2015
Tested: not known to the authorities
Basic education	.025 (.028)	.061* (.033)	.053 (.033)	.003 (.020)
Academic education	−.007 (.031)	.031 (.036)	.001 (.036)	−.004 (.022)
Unknown education	.033 (.026)	.074** (.030)	.047 (.030)	.048** (.023)
Known to the authorities
Age 30–39 years	−.221*** (.049)	−.194*** (.056)	−.188*** (.058)	−.020 (.012)
Age 40–49 years	−.171** (.072)	−.227*** (.080)	−.210** (.089)	−.009 (.022)
Age 50–55 years	−.313** (.133)	−.304** (.146)	−.351** (.178)	−.076*** (.028)
Female	.086*** (.013)	.069*** (.016)	.058*** (.016)	.080*** (.011)
Children 0–2 years	−.028 (.017)	−.004 (.018)	.032 (.020)	.015 (.012)
Children 3–5 years	−.036** (.017)	.009 (.019)	.011 (.020)	−.013 (.011)
Children 6–12 years	−.041*** (.011)	−.027** (.011)	−.038*** (.011)	−.012* (.007)
Children 13–17 years	.041** (.019)	−.009 (.017)	−.003 (.018)	.013 (.010)
Single	−.057*** (.016)	−.067*** (.020)	−.062*** (.019)	−.062*** (.013)
Africa	.165 (.458)	−.454*** (.144)	−.423** (.168)	−.160*** (.052)
Asia	−.010 (.798)	−.748*** (.140)	−.786*** (.121)	−.164*** (.048)
N	15,571	14,323	15,564	21,476
F	1.30	2.37	1.78	3.66
Pr > F	.27	.07	.15	.01

Standardised share of co-nationals in the first municipality on characteristics, origin and cohort fixed effects; SEs clustered by family. F-test: education only. Replication: Foged et al.’s sample definition on our data, arrivals 1987–1998. The last two columns are our own frame, for the two allocation regimes: the Danish Refugee Council’s placement up to 1998, and municipal quotas under the Integration Act from 1999. * p < .10, ** p < .05, *** p < .01.

With the corrected education source, the replication has moved most of the way towards their result: the joint test falls from 4.22 to 2.37 (p = .07), and on our own frame from 6.29 to 1.78, which no longer rejects. Basic education, which used to be the problem at +.06, is now .053 and .003 and insignificant. What is left is the unknown-education category: +.074 in the replication, +.048 in the 1999–2015 regime, both significant. That is the category the source filter creates, so it may be telling us about who has no usable Danish education record rather than about placement — but it is also why the second regime now rejects, F = 3.66 against 0.17 before the correction. So the clean-second-regime claim from last week does not survive. Their column 3 (employment rate of non-Western immigrants) needs municipal employment data we do not have.

Permanent residency

	Arendt, Dustmann & Ku (2025)			Replication, asylum permits			Our sample
	Treated	Control	Difference	Treated	Control	Difference	Treated	Control	Difference
Male	.56	.61	−.05 (.04)	.57	.64	−.069*** (.026)	.41	.46	−.045* (.023)
Age (years)	32.70	33.30	−0.60 (0.74)	32.69	33.27	−0.58 (0.46)	33.04	33.05	−0.01 (0.40)
Married†	.56	.54	.02 (.04)	.62	.67	−.051** (.025)	.72	.77	−.055*** (.021)
Any children	.54	.44	.10*** (.04)	.61	.58	.025 (.026)	.71	.68	.027 (.022)
Country of origin
Afghanistan	.12	.13	−.01 (.02)	.11	.20	−.093*** (.018)	.19	.20	−.008 (.019)
Iran	.09	.03	.06*** (.02)	.07	.07	.001 (.013)	.06	.06	.004 (.011)
Iraq	.03	.08	−.05*** (.02)	.05	.13	−.087*** (.014)	.13	.25	−.129*** (.018)
Myanmar	.21	.08	.13*** (.03)	.12	.04	.087*** (.015)	.10	.03	.071*** (.012)
Somalia	.06	.07	−.01 (.02)	.03	.04	−.003 (.010)	.04	.04	−.001 (.009)
Former Yugoslavia	.09	.03	.06*** (.02)	.24	.18	.061*** (.022)	.19	.14	.049*** (.018)
Other countries	.41	.58	−.17*** (.04)	.38	.35	.034 (.025)	.29	.28	.012 (.021)
Individuals	314	453		575	953		722	1,186

Treated: arrived Jan–Oct 2004; control: Jan–Oct 2003. Arendt et al.: Table 1; differences and SEs computed from their means, SDs and group sizes. Replication and our sample: the same variables computed by the same code, so all three columns are comparable row by row. Replication uses their sample definition on our data, asylum permits only, as a stand-in for their filter on asylum applications after 28 February 2002 (data we do not get — it is held by the ministry, not DST). Our sample: 18–55 at entry, in Denmark in 2024, all permit types. † Arendt et al.: legally married; ours: married or registered partnership. * p < .10, ** p < .05, *** p < .01.

Arendt et al.’s own cohorts are not balanced on origin: Myanmar, Iran and Iraq shares differ significantly (computed from their Table 1). Restricting our replication to asylum permits brings it close to their sample on men (.57/.64 vs. .56/.61) and age (32.6/33.2 vs. 32.7/33.3), and reproduces the direction of their origin differences (more from Myanmar, fewer from Iraq among the treated). It is still twice their size (1,539 vs. 767) and has more former Yugoslavs: without the application dates we cannot drop people who applied before 28 February 2002. With family-reunified refugees included (N = 2,200), the share of men falls to .43/.48.

Sampling DK-born children of refugees

Part 2 of 3

Welfare cut and language training: children and marriage

	Welfare cut (1 Jul 2002)			Language training (1 Jan 1999)
	Mean	Effect	+ controls	Mean	Effect	+ controls
Births registered in Denmark†
All births after the permit	1.40	−0.35*** (0.13)	−0.30*** (0.11)	1.36	−0.03 (0.09)	0.00 (0.07)
births 1–5 years after the permit	0.54	−0.07 (0.07)	−0.08 (0.05)	0.52	−0.04 (0.05)	−0.02 (0.04)
Years from permit to first birth‡	3.97	−0.13 (0.40)	−0.04 (0.27)	4.11	0.13 (0.34)	0.59** (0.27)
Births under 2500 g	.028	.003 (.015)	.002 (.016)	.026	−.004 (.015)	−.004 (.016)
Mean birth weight, g‡	3,404	33 (70)	60 (68)	3,418	−53 (54)	−77 (53)
Children born before the permit	1.64	0.14 (0.18)	0.03 (0.07)	1.70	−0.22* (0.12)	−0.18*** (0.04)
Children living in Denmark in 2025§
Born in Denmark	1.37	−0.32** (0.13)	−0.25** (0.11)	1.34	−0.07 (0.10)	−0.06 (0.07)
both parents immigrants	1.34	−0.33** (0.13)	−0.26** (0.11)	1.30	−0.08 (0.10)	−0.07 (0.07)
a Danish-born Danish-citizen parent	0.03	0.02 (0.02)	0.02 (0.02)	0.04	0.01 (0.02)	0.01 (0.02)
born 1–5 years after the permit	0.51	−0.06 (0.06)	−0.07 (0.05)	0.49	−0.04 (0.05)	−0.02 (0.04)
Born abroad after the parent arrived	0.02	−0.02* (0.01)	−0.02 (0.01)	0.03	0.02 (0.01)	0.02 (0.01)
5 years after the permit
Married	.768	.010 (.041)	−.014 (.020)	.798	−.013 (.028)	−.022 (.018)
Spouse registered in Denmark¶	.653	.010 (.048)	−.026 (.030)	.733	−.004 (.029)	−.014 (.020)
came by family reunification	.187	−.016 (.029)	−.024 (.029)	.274	−.029 (.031)	.011 (.022)
is a refugee	.416	.052 (.052)	.022 (.033)	.399	.013 (.039)	−.028 (.027)
Danish-born or other immigrant	.051	−.025* (.015)	−.024 (.015)	.060	.012 (.013)	.003 (.013)
Married, spouse not in Denmark	.115	.000 (.024)	.013 (.024)	.065	−.008 (.014)	−.008 (.015)
Refugees	4,176			4,671

Discontinuity at the reform date, ±548 days, SEs clustered by date; controls: pre-treatment characteristics incl. Middle East. § Children living in Denmark in 2025 with a parent in our sample. ¶ Spouse ID in that year’s population register. * p < .10, ** p < .05, *** p < .01.

The birth register now carries the fertility results. Refugees have 0.55 births in the five years after the permit. The welfare cut lowers that by 0.09 (SE .05 with controls, −0.09 SE .07 without) — but over the whole period they have 1.40 births and lose 0.31 (SE .11, p = .005). So the effect accumulates rather than being concentrated in the first years. It is not children leaving: in the same 1–5 year window the birth register gives −0.090 and the 2025 stock of those same children −0.077, so attrition is there (0.548 births, 0.515 still here) but it does not differ across the cutoff. Children born before the permit are balanced at the welfare cutoff (+0.11, SE .18), a useful placebo, birth weight does not move at either cutoff, neither the share under 2500 g (.002, SE .014) nor the mean (+44 g, SE 68; language −47, SE 53), on a mean of 3,400 g. Child deaths are too rare to test — under one per hundred births — and the estimates exceed the base rate, so they stay in the log. Language training: no change in the number of births; the first birth comes half a year later, but only with controls (+0.55, SE .27; +0.05 without), so that one should not be pushed. The same caution applies to the −0.18 on children born before the permit: the controls include the number of children at entry, which is nearly the same variable; raw it is −0.19 (SE .12). For the sampling question: the welfare cut changes how many children are born, so a sample of children is shaped by the reform.

Is the drop in children about spouses?

	Welfare cut (1 Jul 2002)			Language training (1 Jan 1999)
	All	Spouse not abroad	Spouse abroad	All	Spouse not abroad	Spouse abroad
Births and children
All births after the permit	−0.35*** (0.13)	−0.27** (0.14)	−0.73* (0.40)	−0.03 (0.09)	−0.01 (0.09)	−0.25 (0.36)
births 1–5 years after the permit	−0.07 (0.07)	−0.04 (0.07)	−0.22 (0.14)	−0.04 (0.05)	−0.03 (0.05)	−0.09 (0.19)
Children in Denmark in 2025	−0.32** (0.13)	−0.28** (0.14)	−0.49 (0.39)	−0.07 (0.10)	−0.06 (0.10)	−0.21 (0.34)
both parents immigrants	−0.33** (0.13)	−0.31** (0.14)	−0.47 (0.40)	−0.08 (0.10)	−0.06 (0.10)	−0.34 (0.33)
a Danish-born Danish-citizen parent	0.02 (0.02)	0.02 (0.02)	−0.02 (0.03)	0.01 (0.02)	−0.00 (0.02)	0.13 (0.12)
Born abroad after the parent arrived	−0.02* (0.01)	−0.03** (0.01)	0.02 (0.06)	0.02 (0.01)	0.02 (0.01)	0.04 (0.07)
5 years after the permit
Married	.010 (.041)	.014 (.047)	.002 (.075)	−.013 (.028)	−.006 (.030)	−.095 (.097)
Spouse registered in Denmark	.010 (.048)	.016 (.048)	−.028 (.096)	−.004 (.029)	.005 (.030)	−.170 (.116)
came by family reunification	−.016 (.029)	−.016 (.031)	−.016 (.086)	−.029 (.031)	−.019 (.032)	−.091 (.128)
Married, spouse not in Denmark	.000 (.024)	−.002 (.020)	.029 (.093)	−.008 (.014)	−.012 (.014)	.075 (.095)
Refugees	4,176	3,628	548	4,671	4,286	385

Discontinuities without controls. “Spouse abroad”: married in the first register year, no spouse registered in Denmark. * p < .10, ** p < .05, *** p < .01.

If the welfare cut reduced births because spouses could not come, the drop should sit with refugees who arrived married with the spouse abroad, and their spouses should arrive less often. The first half now looks better than it did: without controls the spouse-abroad group (551) loses 0.65 births over the whole period (SE .41) against 0.31 (SE .14) for everyone else, and 0.21 (SE .14) against 0.06 in the first five years — point estimates twice the size, the right sign, but standard errors three times as wide, so the two groups cannot be told apart. The second half does not: their spouses arrive just as often (married .004, spouse in Denmark .005, reunified −.003, all with SEs near .09). Language training, spouse-abroad group (384): spouse in Denmark −.25 (SE .12) and married −.18 (SE .10) — the one place in the table where something moves, on 384 people and with no correction for the number of tests on this slide.

Sampling design

Part 3 of 3

We can send invitations to 60.000 people

	Refugees			Their Danish-born children
	All	Treated	Control	All	Treated	Control
Placement 1986-1998	15,576 (14,490)	–	–	22,651 (21,307)	–	–
Placement 1999-2015	21,495 (17,134)	–	–	4,156 (1,350)	–	–
Language training 1999	4,680 (2,223)	2,576 (1,206)	2,104 (1,017)	2,903 (781)	1,421 (387)	1,482 (394)
Welfare cuts 2002	4,176 (1,153)	1,602 (1)	2,574 (1,152)	1,940 (247)	483 (0)	1,457 (247)
Permanent residency 2003/4	1,908 (509)	722 (282)	1,186 (227)	784 (110)	241 (65)	543 (45)

Everyone still registered in Denmark at the latest available year: refugees in each policy’s estimation window, and their children born in Denmark, alive here in 2025 and at least 18 years old. In brackets: those exposed to this policy only, that is, not in the treatment or control group of any other policy. Placement was assigned as a continuous share of co-nationals in the municipality, so it has no arms. A child counts once per policy, whichever parent links them to it. The second table counts refugees who fall in both windows; every pair not shown shares nobody — the two placement regimes are disjoint by construction, and the language reform meets neither the welfare cut nor permanent residency.

Refugees in both windows	Placement 1986–1998	Placement 1999–2015	Welfare 2002
Language training 1999	1,086	1,371
Welfare cuts 2002		2,473
Permanent residency		849	882

This is the sampling frame the whole talk has been building towards, and the brackets are the point. Take the welfare cut: 1,602 treated refugees, of whom exactly one is not also in another policy’s window, and none of their 483 children. Those people arrived in 2002 and 2003, so they are also under municipal quota placement, and the 2003 arrivals are permanent-residency controls as well. The same squeeze, less extreme, hits everything below the first row: language training keeps about 1,200 of 2,576 treated, residency about 500 of 1,908. The two policies with room to breathe are the ones at the edges of the calendar — placement before 1999, which nothing else overlaps, and to a degree the language reform, whose controls arrived before the quota system began. Second point: the children column. The 1986–1998 placement cohorts have 22,700 adult children in Denmark; the 1999–2015 regime, 4,156; the residency cohorts, 784. Their children are simply younger, and we are counting those who have turned 18. So the cleanest design, quota allocation from 1999, is also the one whose second generation we cannot survey yet — and that tension is what the sampling design has to resolve.

Thank you

Merlin & Teresa

Permanent residency: does a donut help?

	Dropped on each side of the changeover
	None	3 months	6 months	9 months
Age at entry
18–29 years	.016 (.023)	−.001 (.029)	−.013 (.037)	−.101 (.062)
30–39 years	−.029 (.023)	−.007 (.029)	.011 (.037)	.068 (.065)
40–49 years	.007 (.019)	−.007 (.023)	−.022 (.030)	.037 (.054)
50–55 years	.006 (.010)	.015 (.013)	.024 (.018)	−.003 (.025)
Children at entry
0–2 years	.037 (.025)	.033 (.031)	.033 (.040)	.076 (.072)
3–5 years	−.031 (.023)	−.031 (.029)	−.031 (.033)	−.030 (.046)
6–12 years	−.023 (.048)	−.034 (.062)	−.070 (.074)	−.105 (.123)
13–17 years	.115*** (.042)	.123** (.052)	.110* (.067)	.195 (.129)
Female	.045* (.023)	.033 (.029)	.007 (.038)	.027 (.066)
Married	−.055*** (.021)	−.070*** (.026)	−.079** (.034)	−.083 (.061)
Region of origin
Middle East	−.120*** (.023)	−.185*** (.029)	−.188*** (.038)	−.281*** (.064)
Europe	.079*** (.020)	.093*** (.025)	.073** (.031)	.213*** (.056)
Africa	.007 (.016)	.051** (.021)	.075*** (.029)	−.006 (.048)
Asia	.034** (.017)	.035** (.016)	.027 (.020)	.051 (.038)
Other region	.001 (.003)	.006 (.004)	.012* (.007)	.024 (.017)
Joint F (p)	3.63 (< .01)	3.61 (< .01)	2.51 (< .01)	2.00 (.03)
Joint F, adding Middle East	6.30 (< .01)	6.33 (< .01)	3.76 (< .01)	4.93 (< .01)
Individuals	1,908	1,261	819	267

Difference between the 2004 and 2003 cohorts, robust SEs, as on the previous slide. Each column drops more of the weeks closest to the changeover, where people whose asylum application fell under the old rules are most likely to be mixed in with people under the new ones. Widening the gap also pushes the two cohorts further apart in calendar time and cuts the sample, so it trades one bias for another rather than removing it. * p < .10, ** p < .05, *** p < .01.

The donut does not rescue the design. If the cohort differences came from people near the changeover being misclassified, they should fade as the gap widens. They grow: Middle East 212.12, 212.18, 212.18, 212.28; married 212.055 to 212.084; Europe +.08 to +.21. The joint test rejects at every width — F = 3.69, 3.58, 2.42, 1.99, all with p < .05, and 6.42 to 4.94 once Middle East is added. The F falls only because the sample falls, from 1,909 to 268; the coefficients themselves get bigger, so this is lost precision, not improving balance. The conclusion is that the 2003 and 2004 cohorts genuinely differ in who they contain 014 the missing asylum application dates are not what is driving it, and no sample restriction we can make from the permit date will fix it. That is the argument for measuring treatment instead of assuming it: the permanent-residency register tells us who actually obtained permanent residency and when, which turns this into a fuzzy design with a first stage we can estimate.