When economists ignore history
A new paper on apartheid fails to impress
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That the forced migration of black South Africans to the homelands had adverse effects on those relocated would not come as a surprise to students of South Africa – or indeed the millions of South Africans who directly experienced the detrimental impacts of these policies. It was, of course, part intentional: ‘Surplus’ populations were being removed to areas where they could be controlled more easily despite being deprived of educational opportunities. And its effects on education, income and general well-being have been well-documented by both South African historians and economists.
Which is why the publication of the paper ‘Moved to Poverty? A Legacy of the Apartheid Experiment in South Africa’ by Bladimir Carrillo, Carlos Charris and Wilman Iglesias in the November issue of the American Economic Journal: Economic Policy attracted my interest. In it, the authors investigate the long-term impacts of apartheid-era policies that forcibly relocated black South Africans to homelands, analysing how these relocations affected educational attainment, labour earnings, and employment rates in adulthood. Using a cross-cohort identification strategy that leverages the staggered timing of homeland establishment, the authors find that moving to homelands during childhood significantly reduced individuals’ education levels by approximately 0.55 years or 11% of the sample mean, decreased the likelihood of employment by 20%, and reduced adult income by 5.6%.
There is much econometrically to admire in the paper. The methods used to arrive at the results are innovative and implemented with all the sophistication you would expect of an economics paper in a top journal.
But there is also something missing from the paper: a knowledge of the historical context. And, as I will argue here, this is a great example of where history really matters because, had the researchers properly engaged with the history of forced removals (or had the editors chosen referees with some knowledge of South Africa), they would have realised that their research question is fundamentally uninteresting, their results tenuous, and their policy implications weak.
It doesn’t take the reader long to notice the lack of history. Just turn to the reference list, and you’ll notice remarkably few papers on South Africa.
Where to start? A paper on the homelands would be expected to cite at least some general histories of the homelands policy, including Horrell (1973), Butler, Rotberg and Adams (1977), Southall (1983), Platzky and Walker (1985), Savage (1986), Unterhalter (1987) and the voluminous material related to the Second Carnegie Commission into Poverty, edited by Francis Wilson (1984). Simkins (1983), a paper the authors do cite, is not an obvious go-to for historiography on the homelands. Such histories could have provided more detail about the process of moving to the homelands – many delayed going, for example – a fact that the authors deal with competently in the empirical section but never mention in the context section.
Economists have studied the homelands and their consequences too, investigating residency in the homelands’ effects on migration (Posel 2004; Von Fintel and Fourie 2019), employment (Leibbrandt, Bhorat and Woolard 2001; Lochmann, Rao and Rossi 2022), poverty and inequality (Woolard and Klasen 2005; Van der Berg 2011), and education (Van der Berg 2007), to name just a few. Economic historians, unsurprisingly, have also delved into the economics of apartheid (Mariotti and Fourie 2014; Mariotti 2015).
One consistent finding is the heterogeneous effects within and between the homelands. De Wet and Leibbrandt (1994), for example, consider two homeland villages in Ciskei, noting: ‘There can be no doubt about the impoverishing effects of the homeland policy. However, the fact that its impact has not been evenly felt on the ground remains important for post-apartheid policy discussions. Some communities have been better placed than others to minimise its destructive interventions and to benefit from the limited opportunities which it has opened up.’ Spaull (2016) notes: ‘While these four schools may have been relatively representative of primary schools in the Bophuthatswana homeland, one should be cautious of extending the generalisability to schools in other homelands, because Bophuthatswana may have been quite different to the other homelands.’
There are more specific histories, too, from which the paper would have benefited. Education, as the historian Linda Chisholm’s research shows, varied considerably in the Bantustans; while often worse than in urban areas, it was not uniformly so, and importantly, Bantustans were not obligated to implement Bantu Education like schools in ‘white South Africa’ (Chisholm 2013; 2018). The authors also fail to consider the significance of 1976, when urban children poured into Bantustan schools, as their parents tried to protect them from the political unrest radiating out from the Soweto Uprising, as is evident in the work by Mathabatha (2004), Lekgoathi (2007) and Philips (2015). In short, education quality is ignored. Does the Bantu Education Act coincide with the education timing of individuals in the sample? Yes, it does. Does this matter? It is possible to compare educational attainment by year across space and time – as the authors do when they impute an age of arrival – when there are varying levels of quality across space but also across time. Eriksson (2014) is a good start.
Neglecting education dynamics has implications for the main results of the paper. If the Bantu Education Act causes changes within ‘white South Africa’ that may affect the movers before they move, then we do not know whether they got less education because they were less prepared outside the homelands before they moved or whether they got less education within the homelands because they moved.
A deeper historical context would have also exposed what I consider the main issue with the paper: that the authors compare black South Africans who move to the homelands with those already in the homelands. This is not the most interesting control group; what we would really like to know, surely, is whether those forcibly removed did better or worse than those who remained behind.
That is a question, of course, the data cannot answer. But it is not even clear that the data, as it is, can answer the less interesting question the authors ask of it. They use complete census data from 1980, 1985, and 1991 but note that these files “exclude a few homelands (listed in online Appendix Table A.1)”. This omission seems vitally important for a study specifically focused on homelands, especially, as historians have shown, that there is large heterogeneity between homelands. What proportion of homeland dwellers are excluded from the estimation? How would excluding several non-random homelands affect the external validity of the results?
If the education findings are questionable, then the findings about income are even more so. Income has been notoriously poorly measured across multiple data sets in South Africa. For example, census incomes are reported in bins, though the authors never mention this inconvenience. Their results suggest that income is accurately measured. They do not mention how they deal with bins.
Having uncovered the extent to which the newly arrived migrants underperform native residents of the homelands, the authors then make several policy proposals. The paper tries to add to the ‘moving to opportunity’ literature inspired by Raj Chetty and friends, who investigate the long-term outcomes of American families who moved from high-poverty neighbourhoods to lower-poverty areas, demonstrating significant improvements in children’s earnings, educational attainment, and long-term economic self-sufficiency. The authors then make a strange choice. They prioritise a discussion on how their findings might influence housing policies in Chicago rather than what the implications of their results are for South Africa’s development. I would think that the situation in South Africa – relocating people sometimes hundreds of miles to overcrowded reserves far from employment opportunities – is quite different from constructing housing projects within a city, rendering the policy implications, sadly, arbitrary and inconsequential. Ken Opalo has recently written a great critique of such research.
‘Moving to opportunity’ is a missed opportunity. It also provides further evidence that the economics field is split into a two-tier system, with the upper tier dominated by top journal editors and referees who lack engagement with the historical context of their research topics. They also show little interest in exploring work by economists outside their elite circle or by historians from any tier. Despite the fact that the acknowledgements section of the paper includes notable development economists, the paper overlooks a wealth of literature on South Africa’s economic development and South African history, suggesting either an oversight or a deliberate exclusion.
The authors claim a scarcity of research on apartheid’s legacy – the paper ‘represents one of the first rigorous, empirical analyses of a significant historical event that has not received much attention in the economics literature’ – but this appears to be a narrow view confined to the top economics journals. It hints at academic colonialism, characterised by a focus on achieving publication in prestigious journals at the expense of recognising existing, high-quality research. This is particularly ironic given the authors’ backgrounds in regions historically subject to such exclusion.
Unfortunately, the paper teaches us little that is new about South Africa, past or present, and given the failed attempt to link this to an international literature, even less about economics.
‘When economists ignore history’ was first published on Our Long Walk. I want to thank the ten anonymous scholars who provided referee comments on the original paper. All errors, though, are my own. The image was created with Midjourney v6.
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Amen!