The UK was one of only three countries that granted free movement of workers to accession nationals following the enlargement of the European Union in May 2004. The resulting migration inflow, which was substantially larger and faster than anticipated, arguably corresponds more closely to an exogenous supply shock than most migration shocks studied in the literature. We evaluate the impact of this migration inflow – one of the largest in British history – on the UK labour market. We use new monthly micro-level data and an empirical approach that investigates which of several particular labour markets in the UK – with varying degrees of natives’ mobility and migrants’ self-selection – may have been affected. We found little evidence that the inflow of accession migrants contributed to a fall in wages or a rise in claimant unemployment in the UK between 2004 and 2006.
We acknowledge and thank the financial support of the Department for Work and Pensions. We are also grateful for the data provided. Views expressed in this paper are not necessarily those of the Department for Work and Pensions or any other Government Department.
A special thanks to Alan Manning, Barry Chiswick, Carlos Carrillo-Tudela, Gianni De Fraja, Ian Preston, Jennifer Hunt, Juan Jimeno, Kevin Lee, Martin Hoskins, Steve Hall, James Rockey and Tim Hatton. Mathew Hentley, David Finchley, and Jag Athwal provided invaluable research assistance. Also, thanks to comments from discussants and participants in various conferences and seminars.
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Our results are in line with evidence in the international (mainly US) literature of little or no effect on employment and wages (Chiswick 1980; Grossman 1982; Card 1990, 2005 and 2007; LaLonde and Topel 1991; Altonji and Card 1991; Pischke and Velling 1997; Friedberg 2001; Dustmann, Fabbri, and Preston 2005; Dustmann, Frattini, and Preston 2007; Manacorda, Manning, and Wadsworth 2006; Carrasco, Jimeno, and Ortega 2008), though in contrast with other evidence of more adverse effects (Borjas 2003 and 2006; Angrist and Kugler 2003; Orrenius and Zavodny 2007). As we discuss in Sections 3–5, the disagreement in the literature is underlined by an ongoing debate on identification issues arising from natives’ mobility and migrants’ self-selection (see for example Chiswick 1991; Borjas 1999; Card 2001).
For example, while 24.1% of those registering in the WRS in the first two months state “entry date” before January 2004 (these include students, illegal workers, self-employed, etc.), this goes down to 2.1% after 1 year (Home Office 2005). These figures are produced aggregating the data by “application date”, whereas others have also used “entry date” (Gilpin et al. 2006). As the typical accession migrant enters the UK, finds a job, and then applies to the WRS, we instead aggregate the data using “start of work date” to best capture labour market effects and to skew from identification problems associated to using “entry date” or “application date”. (For completeness, however, we re-estimated Equation  in Section 3 aggregating the data by “entry date” and obtained qualitatively similar results.)
A caveat with the WRS is that it measures inflows only, and thus we cannot calculate the associated netflow and stock. This is because the WRS records jobs, not people: migrants leaving the UK are not counted, whereas migrants re-entering the UK are double counted. Blanchflower, Saleheen, and Shadforth (2007) analyze A8 migration figures across several data sources and conclude that a stock of 500,000 migrants by late 2006 is likely to be an upper bound. Pollard, Latorre, and Sriskandarajah (2008) and Coats (2008) provide similar analysis and conclude that outflow is not zero, in line with evidence on return migration (LaLonde and Topel 1997). We discuss how measurement error in the WRS might affect our estimates in detail in Sections 2.1 and 4.2. Another caveat with the WRS is that the self-employed are not required to register (although they are a minority that already had relative access to EU labour markets).
We define and , where is the number (stock) of JSA claimants, is the number (stock) of WRS migrants, and is the working age population. As discussed in Section 2, whereas we observe the stock of claimants and can calculate the netflow of claimants as ; we do not observe the stock of migrants. We therefore re-define the netflow of migrants as , where is inflow and is outflow of migrants. As we do not observe outflow, we again re-define , as is common in the literature (see for example, Card 2001; Dustmann and Glitz 2005) and interpret it as a variable in differences. Similarly, we define the native (netflow) rate and , where is inflow and is outflow of natives. We also run robustness checks where our migration and unemployment variables in eq.  were not normalised (i.e. re-defining and ) and found qualitatively similar results.
As in Gilpin et al. (2006), we experimented with two types of dynamics (lagged migration rate and lagged claimant unemployment rate), which, however, did not qualitatively alter our results. Although dynamics allow for lagged adjustments due to slow responses in employment, migration effects are generally expected to be lower in the longer than in the shorter run (Altonji and Card 1991; Dustmann, Fabbri, and Preston 2005).
The appropriate weight here is the sample size used to calculate the dependent variable (working age population), but our estimates were also robust to using total population as weight instead – which reduces concerns of a potential correlation between the weight and the dependent variable affecting the results. (Also, as discussed in Section 2.1, we run robustness checks where our unemployment and migration variables were not normalised and found qualitatively similar results.) Our estimates were also robust to using, in turn, April 2004 working age population and April 2004 total population as time-invariant weights (see Card 2001; Borjas 2006).
Our three groups comprise: those with a degree and above, those with GCSE and below, and those in between. Robustness checks showed qualitatively similar results when the last was omitted.
We re-estimated Equation  at the district and year level – to check whether variation is greater when the data is aggregated at the yearly instead of monthly level – and the results remained qualitatively the same.
Most studies for the UK use data from the LFS, where migration analysis below the region and quarter level is not feasible (see Section 2). The implicit assumption in these studies is that there are 12 regional closed labour markets in the UK, where the whole of London is treated as one data point – even though London has 33 districts, where 41% (17%) of all (WRS) migrants are unevenly distributed. We overcome this weakness in the literature by aggregating the data at finer (district and county) levels.
Although WRS migrants overwhelmingly concentrate in low-skilled elementary occupations, for completeness we also run robustness checks for middle and high-skilled occupations and found no evidence of adverse effects.
While it is possible that some (more able or better informed) WRS migrants studied their UK employment probabilities and applied for jobs prior to migrating, the vast majority of them arrived in the UK without a job and without much knowledge of the labour market or the language (see Section 2). For example, the average number of days between entry and date of start of work is 116.3; 42.4% of WRS migrants were employed within 30 days, a further 11.2% within 60 days, and the other half took longer than 2 months to find work.
It is possible that the pre-accession regional distribution is itself endogenous. London and the South East have more dynamic economies than other regions, though they also have higher unemployment (see Table 1). These are areas traditionally associated with migration from all countries (40% of all migrants reside in London).
We performed robustness checks restricting our sample to the first 6 and 12 months and found no evidence of more adverse effects (also see Gilpin et al. 2006). We also performed robustness checks restricting our sample to London, the South East and East of England and found no evidence of more adverse effects (see Section 4.1.1).
It is worth noting that, during the sample period, the number of WRS migrants eligible and in receipt of JSA is negligible. This is because A8 nationals only had access to certain social security benefits, such as the JSA, 2 years after registration in the WRS (Home Office 2004) (see Section 2). For similar reasons, the number of other recently arrived non-eligible non-A8 migrants is also negligible; earlier eligible migrants are treated as UK residents (see Sections 2 and 6). Furthermore, our variable of interest is JSA claimant unemployment, as opposed to broader (ILO) unemployment or employment, and this reduces further concerns of simultaneity bias.
Finding valid instruments really is very hard, especially because, ideally, they need to vary at the month and district level. This largely constrained us to instruments derived from our datasets. Obvious instruments were lags of our migration rate. We also experimented with lags of the entry-migration rate, where we use “entry date” to define the instrument and “start of work date” to define the variable of interest (see Section 2). We then defined predicted migration rates using the A8 distribution in the 1991 and 2001 Census (Card 2001; Dustmann, Frattini, and Preston 2008). We also experimented with instruments derived from Civil Aviation Authority (CAA) data, such as a flight indicator and its interaction with the distance between a particular A8 country and a particular UK district; the minimum, maximum and average air fare prices; the number of air fares (one way and return); and the number of passengers travelling (arriving and departing) between A8 countries and UK districts. Although the associated results were qualitatively similar, these instruments were less relevant and the estimates less precise. We further used other instruments suggested in the literature, such as historic migration rates, house prices, vacancy rates and temperature (Hatton and Tani 2005; Saiz 2007; Hunt 1992). However, the poor quality of the data and/or the lack of variation at the district and month level cast doubt on the results.
Several skill definitions have been used in the literature: occupation, education, education-experience, and so on (see for example Card 2001; Borjas 2003). Occupation is measured more accurately than education and experience. Firstly, the extent and quality of education varies across countries. Therefore, migrants and natives in the same education cell may have different skills and compete for different jobs. Secondly, occupation measures the effective reward that migrants obtain, after usual skill downgrading due to language or other labour market barriers. Thirdly, there is evidence that natives and migrants are imperfect substitutes within education groups in the UK (Manacorda, Manning, and Wadsworth 2006). As discussed in Section 4.1, identifying accurately who competes with whom is crucial, as poor skill group allocation results in poor identification.
Our results using sought occupation, which better captures labour market effects, were also robust to using usual occupation instead.
Unlike the JSA unemployment data, which contained a negligible number of WRS migrants, the ASHE wage data contains both natives and WRS migrants, as discussed in Section 2. Thus, we estimate the effect of the WRS migration shock on the wages of both natives and WRS migrants. In other words, it is possible that simultaneity bias might be more of a concern in our wage models. Nevertheless, this is a common feature of employment and wage data in most migration studies in the literature and what is actually uncommon is to have a relatively simultaneity-bias-free measure of unemployment, as we do (see Footnote 16). The drawback here is that our wage estimates were not subject to instrumental variable robustness checks. (They were robust, however, to natives’ mobility (omitted) variable bias, when we controlled for lagged working age population growth and natives’ netflow rate, as in Section 4.) This is due to data limitations – since our wage data is not as rich as the claimant unemployment data – but also because there was little evidence of severe endogeneity bias (deriving from omitted variable bias or measurement error bias) in Sections 4.1–4.3. As a result of this drawback, a cautious view is that our wage estimates derive from a descriptive (not causal) model.
Claimant unemployment effects were not substantially more adverse when we excluded machine operatives (see Table 5), as might have been expected if demand factors attracted both migrants and (claimant) natives (see Section 2.1). An explanation here is that most such demand factors were controlled for in the model. Another explanation is that natives other than claimants were attracted to machine operative’s demand shock.
Our insignificant 0.323 and 0.438 estimates for the 25th and 50th percentiles are larger than their 0.136 and 0.234 insignificant estimates (their associated instrumented estimates are an insignificant 0.211 and a significant 0.660). Our insignificant 0.110 estimate for the 10th percentile is again close to their insignificant uninstrumented –0.094 estimate (their associated significant instrumented estimate is –0.516), although in the opposite direction. One explanation here is that the minimum wage was in force and increasing throughout the period we study, possibly mitigating or offsetting more adverse wage effects for lower paid workers, as we discuss below. One fruitful avenue of research is to extend the sample period in Dustmann, Frattini, and Preston (2007) accordingly.
©2014 by Walter de Gruyter Berlin / Boston