Congress passed the Fair Housing Act as Title VIII of the Civil Rights Act of 1968, Public Law 90-284, signed by President Lyndon B. Johnson on April 11, 1968, and rebuilt its enforcement machinery twenty years later in the Fair Housing Amendments Act of 1988, Public Law 100-430, signed by President Ronald Reagan on September 13, 1988. The statute bars discrimination in the sale, rental and financing of housing on the basis of race, color, national origin and religion, with sex added by the Housing and Community Development Act of 1974, Public Law 93-383, and disability and familial status added by the 1988 amendments. Any honest accounting of what the law achieved has to begin with a distinction the enforcement record forces on the reader. The 1988 amendments supplied the enforcement scheme under which effects are measured: administrative complaints heard by administrative law judges, civil penalties, and injunctive authority for the Department of Justice. Before that change the original 1968 act depended largely on private lawsuits and a Department of Housing and Urban Development that could investigate and conciliate but not compel, which is why analysts date serious enforcement to 1988 rather than 1968. The question this article answers is the one the evidence can actually support: what measurably changed in residential segregation, homeownership and detected discrimination in the decades after enactment, which study series supplies the causal evidence, and what did not change despite the statute. Readers looking for the provisions themselves, the cases that construe them, and the full enforcement record should consult the companion pieces on this site: the provisions evaluated here are laid out in the complete guide to the 1968 act, the doctrine that shapes what can be proved is traced in the Supreme Court cases, and the lending record sits beside the Community Reinvestment Act guide.

The short answer, stated before the evidence that earns it, is that the Fair Housing Act worked best at the job it was written to do and least at the job later observers wished it had done. Paired testers sent into housing markets by four federal studies between 1977 and 2012 found that the bluntest form of discrimination, the flat refusal to do business with a minority homeseeker, declined from common to rare. The standard measure of black-white residential separation fell from roughly 80 percent in 1970 to roughly 55 percent in 2010, the lowest level since 1920, and declined in every one of the nation’s 85 largest cities. The largest fair lending settlements in the country’s history at the time, $335 million against Countrywide in December 2011 and $175 million against Wells Fargo in July 2012, followed the financial crisis and put dollar figures on patterns of steering and pricing discrimination the statute was designed to reach. Against those gains stands the field’s most sobering statistic, and it must be stated with the precision the record demands because careless versions of it circulate widely. The black homeownership rate stood near 42 percent in 1970 and near 42 percent again in 2015, effectively flat across five decades. Because the white rate moved upward over the same span, the white-black ownership gap did not stand still; it widened, from roughly 25 percentage points in 1970 to roughly 30 percentage points in 2015. The rate is flat. The gap grew. Every rendering that says otherwise, including the familiar claim that the gap is unchanged from 1968, misreads the arithmetic, and this article treats the corrected version as the fact a reader must carry away.

The evidence table below compresses the whole record into five findings, each with its direction, its period, the data series or study behind it, and a rating of how settled the finding is. The sections that follow unpack each finding in full, name every source in prose, and explain the limits of what each measure can and cannot prove. The complaint record that followed the 1988 amendments carries its own surprise: disability, a class added by those amendments, accounted for more than half of all fair housing complaints reported nationwide for calendar 2014, a proportion the National Fair Housing Alliance put at 51.8 percent against 22.0 percent for race. The displacement history that preceded the statute, the federal campaign that cleared neighborhoods in the name of renewal, is covered in the guide to the Housing Act of 1949, and the voucher-based mobility research that became the statute’s most rigorous neighborhood experiment is surveyed in the Section 8 housing voucher guide. What follows is the record, measure by measure, with the names of the scholars, agencies and series that produced it.

The statute whose effects are measured here carries two public law numbers, and the distinction between them organizes the entire article. Public Law 90-284, Title VIII of the Civil Rights Act of 1968, stated the prohibition: discrimination in the sale, rental and financing of housing on the basis of race, color, national origin and religion is unlawful. Public Law 100-430, the Fair Housing Amendments Act of 1988, 102 Statute at Large 1619, codified at 42 United States Code sections 3601 through 3619, supplied the enforcement: the administrative complaint process, the administrative law judges, the civil penalties, and the strengthened Justice Department litigation authority, plus the two new protected classes whose complaints dominate the docket. Effects measured from 1968 are therefore effects of a prohibition that operated for twenty years with weak tools and then for twenty-eight years with strong ones, and any trend that bends after 1988, as the testing series’ later rounds do, has a plausible institutional explanation. The article meets that standard by naming, for every figure, the series, the years, the measure and the publisher, and by stating the limits each source’s own authors placed on it.

The ratings in the final column deserve a precise reading, because they are doing analytical work the prose does not repeat. A settled rating means multiple independent sources converge on the direction of change: the census analyses of Glaeser and Vigdor, Sander, and Logan and Stults all point the same way on black-white dissimilarity, and the four testing rounds all point the same way on the decline of overt refusal. A measurable rating means one authoritative series reports the figure with stated limits: the Alliance’s 2015 Trends Report is the source for the 51.8 percent disability share, and the article reports its aggregation method and its counting caveats alongside the number. A contested rating means the evidence points in different directions depending on the specification: the raw HMDA ratios and the adjusted Boston estimates tell different stories about the size of the lending disparity, and the four testing studies’ methodological differences bar the precise trend comparison their qualitative agreement invites. The table is therefore not a summary of conclusions but a map of evidentiary confidence, and the reader should carry the ratings into every section that follows.

The Five-Finding Evidence Table

The Fair Housing Act’s effects can be summarized in five measurable outcomes, each resting on a named data series. The table gives each outcome, the direction of change, the period covered, the series or study that produced it, and a rating. A finding rated settled rests on convergent evidence from multiple independent sources; a finding rated measurable rests on one authoritative series with stated limits; a finding rated contested is one where the raw evidence and the adjusted evidence point in different directions, or where methodology blocks firm comparison.

Outcome	Direction	Period	Data series or study	Rating
Black-white residential separation	Declined, about 80 in 1970 to about 55 in 2010; high 70s persist in older industrial metros; Hispanic separation rose through the late twentieth century then flattened, Asian separation rose through 2010	1970 to 2010	Decennial census; Glaeser and Vigdor, Manhattan Institute Civic Report No. 66, January 2012; Logan and Stults, US2010 Project, 2011; Iceland, Weinberg and Steinmetz, Census Bureau working paper, 2002	Settled
Black homeownership rate	Flat, about 41.6 to 42.1 percent in 1970 and about 41.5 to 41.9 percent in 2015; gap widened from about 25 to about 30 points	1970 to 2015	Census Bureau CPS/HVS; 1970 decennial census; Collins and Margo, 2001	Settled
Detected overt refusal to rent or sell	Declined sharply; subtler shortfalls in units shown and told about persisted	1977 to 2012	HMPS 1977; HDS1989; HDS2000; HDS2012, HUD	Settled for qualitative trend; numeric cross-study comparison contested
Disability share of fair housing complaints	Majority, 51.8 percent of complaints in calendar 2014, race second at 22.0 percent	Calendar 2014	NFHA Fair Housing Trends Report, 2015 edition	Measurable
Mortgage denial disparity, raw and adjusted	Raw gap about 2.7 to 1, adjusted to about 1.6 to 1 with extensive controls; settlements of December 2011 and July 2012 were the largest and second largest as of their announcements	1990 to 2012	Boston Fed Munnell et al., 1992 and 1996; DOJ settlements December 2011 and July 2012	Contested in raw form; measurable after adjustment with stated limits

The article proceeds in the order the evidence demands. It begins with the instrument, the dissimilarity index, because no segregation figure means anything until the reader knows what the index counts. It then takes the five findings in turn: the long decline in black-white separation and the metros where it stalled, the divergent Hispanic and Asian trajectories, the homeownership rate that did not move and the gap that grew, the four testing studies that supply the causal evidence, the complaint mix the 1988 amendments produced, and the lending record with its raw and adjusted gaps. The evidence table compresses the five into a single view. The Westchester case and the Moving to Opportunity experiment then show the enforcement frontier and the neighborhood frontier respectively, before the article states its claim, answers both overreaches, and closes with what the evidence settles. Every figure in the journey carries its series, its years and its measure; every limit the sources’ authors stated is stated here.

How segregation gets measured

Before any figure in the record can mean anything, the reader needs the instrument that produced it. Residential segregation in the American social science literature is measured above all by the index of dissimilarity, denoted D, a statistic developed by Otis Dudley Duncan and Beverly Duncan in 1955 and given its canonical modern form by Douglas Massey and Nancy Denton in their 1988 Social Forces article on the dimensions of residential segregation. The index compares the distribution of two groups across the neighborhoods of a metropolitan area against the distribution that would hold if every neighborhood mirrored the area’s overall composition. It runs on a scale from 0 to 100, and the Census Bureau’s Housing Patterns appendix states the interpretation plainly: the score is the percentage of one group’s population that would have to change residence so that every neighborhood matched the metropolitan average. A score of zero means complete integration; a score of 100 means complete segregation, with every member of each group living in neighborhoods containing none of the other.

The dissimilarity index is the most quoted of five standard dimensions of segregation, and the other four explain what it cannot see. Massey and Denton’s 1988 article, The Dimensions of Residential Segregation, identified evenness, exposure, concentration, centralization and clustering as distinct axes along which groups can be separated. Dissimilarity measures evenness alone: how uniformly the two groups are spread across neighborhoods. It is blind to spatial arrangement, so a metropolitan area where black and white blocks alternate in a checkerboard can score the same as one where all the black blocks form a single ghetto, and it says nothing about whether the minority population is concentrated in a small land area or pressed into the urban core. The literature converged on dissimilarity not because it captures everything but because it is computable from every census since 1890, it has an intuitive percentage interpretation, and it moves sensibly when neighborhoods change. The Iceland, Weinberg and Steinmetz finding that black segregation declined across all five dimensions between 1980 and 2000 is therefore stronger than a dissimilarity-only result: it says the improvement was not an artifact of one axis.

Geographic grain is the second measurement choice the reader should understand. Census tracts, the unit of the Glaeser and Vigdor analysis, average a few thousand residents; census blocks, the unit of Sander’s corroborating analysis, are far smaller. Finer grains generally produce higher segregation scores, because separation that averages out at the tract level survives at the block level, which is why Sander’s 0.92 to 0.70 block-level decline sits above the tract-level numbers for the same years rather than contradicting them. A reader comparing a tract figure to a block figure without naming the grain will manufacture a disagreement the sources do not contain. The convention in the field is to report the grain alongside the number, and this article follows it: tract-level unless stated otherwise, block-level where Sander’s work is cited.

Massey and Denton, in American Apartheid in 1993, supplied the conventional thresholds the literature still uses: scores from 0 to 30 count as low segregation, 31 to 60 as moderate, and 61 to 100 as high. Scores above 75 are conventionally described as extreme. The same numbers appear in decimal form in some reports, so a score written as 0.70 means the same thing as 70. The index has a second companion measure, the isolation index, which captures the likelihood that a member of a group encounters only members of the same group in the home neighborhood; the two measures can move differently, and the distinction matters because dissimilarity can fall while isolation stays intense if a group’s share of the population is growing. When the sections below report a figure like 55, the reader should hear it as 55 percent of black residents who would have to move to match the metropolitan composition, a number in the moderate band but uncomfortably close to the high threshold, not as an abstraction.

What does a dissimilarity score of 55 mean?

It means that 55 percent of black residents in the measured area would need to change neighborhoods so that every tract matched the metropolitan average, placing the area in the moderate band of the 0 to 30, 31 to 60, 61 to 100 convention while leaving real separation intact.

Black-white separation: the long decline

The central trend in the segregation record is a long, uneven decline in black-white separation from its twentieth-century peak. Edward Glaeser of Harvard and Jacob Vigdor of Duke, in their January 2012 Manhattan Institute Civic Report No. 66, The End of the Segregated Century: Racial Separation in America’s Neighborhoods, 1890 to 2010, analyzed thirteen consecutive census administrations using both the dissimilarity index and the isolation index. Their headline result: national black-white dissimilarity stood near 80 percent in 1970 and near 55 percent in 2010, the lowest level recorded since 1920. Journalist’s Resource, summarizing the report, noted that dissimilarity declined in all 85 of the nation’s largest cities and that segregation kept falling through the 2000 to 2010 decade, with 522 of 658 housing markets recording declines. The direction is not an artifact of one team’s methods. Richard Sander, writing in the University of Chicago Law Review on the policy lessons of partial desegregation, computed average block-level dissimilarity across 60 major metropolitan areas and found it falling from 0.92 in 1970 to 0.70 in 2010, a corroboration at a finer geographic grain than the tract-level census work.

The finding carries a documented counterweight that the article must carry alongside it. The Economic Policy Institute published a widely noted critique of the Glaeser and Vigdor report in January 2012, arguing that the dissimilarity measure masks demographic and economic trends and that isolation remains intense for black residents even as dissimilarity falls. The critique does not overturn the trend; no serious scholar disputes that measured dissimilarity declined. It does caution the reader against reading a 25-point drop as the end of separation, because a growing black population can hold isolation steady while dissimilarity falls, and because the average conceals the metropolitan variation the next section takes up. The responsible reading is the one the literature itself converges on: separation declined substantially from its 1970 peak through the following four decades, the decline touched every large city, and it did not end high segregation in the places where segregation was worst. The reader who quotes the 80-to-55 decline should always name the measure, the years and the source, because a segregation figure without those three attributes is exactly the recurring error this field punishes.

The timing of the decline also matters for any claim about what caused it. The steepest measured drops came in the decades after the statute’s enforcement machinery was rebuilt in 1988, and the literature is careful not to credit the statute alone. Postwar suburbanization, black middle-class growth, the aging of the most rigidly segregated cohorts, and changing white attitudes all moved in the same direction. The statute plausibly accelerated the decline by making overt exclusion costly and by creating the paired-testing apparatus that documented the subtler forms that replaced it, but the census trend by itself cannot apportion credit among causes. An impact article earns trust by refusing to do what its data cannot support, and the causal claim for the segregation decline stays at the level the evidence supports: measured separation fell substantially while a statute aimed at transactional exclusion operated, and the sharpest falls in overt refusal, documented independently by the testing studies, are the channel through which the statute most plausibly acted.

The breadth of the decline deserves emphasis because it answers the objection that the national average is carried by a few Sun Belt metros. Journalist’s Resource, summarizing Glaeser and Vigdor, reported that dissimilarity declined in all 85 of the nation’s largest cities, without exception, and that the decline continued through the 2000 to 2010 decade, with 522 of 658 housing markets recording drops. A trend that touches every large city and four-fifths of housing markets in a single decade is not a compositional artifact. The 2012 report’s other headline, that 2010 marked the lowest black-white dissimilarity since 1920, puts the twentieth century’s arc in perspective: separation rose through the early decades of the century as the Great Migration moved black Southerners into Northern and Western cities that met them with covenants, violence and redlining, peaked around 1970, and then fell for four consecutive decades. The statute took effect near the peak, which is convenient for storytelling and dangerous for causal claims, because a series that peaks will often fall for reasons that have nothing to do with any law.

The Economic Policy Institute’s January 2012 critique of the Glaeser and Vigdor report is the most careful statement of why the headline number should not be oversold. EPI argued that the dissimilarity measure masks the demographic and economic trends running beneath it: black suburbanization, which lowers measured dissimilarity, can coincide with the growth of predominantly black suburbs whose residents remain isolated from white neighborhoods, jobs and resources. Isolation, the companion index Glaeser and Vigdor also computed, remained intense even as dissimilarity fell, because the black share of metropolitan populations was growing over the same years. The critique does not dispute the 80-to-55 decline; it disputes the inference that a 25-point drop in evenness means a 25-point improvement in lived experience. This article carries both the number and the caution, because the reader who repeats the number without the caution will be corrected by the first scholar they meet, and the reader who repeats the caution without the number will miss the genuine change the testing series independently confirms.

Causal modesty is the third obligation this section owes the reader. The literature attributes the decline to no single cause, and the honest list is long: postwar suburbanization and the black middle-class growth that made suburban moves possible, the aging and dying of the cohorts socialized under the most rigid segregation, measurable change in white attitudes toward neighborhood integration, and the statute itself, operating through the enforcement machinery rebuilt in 1988 and the testing apparatus that made subtle discrimination visible and therefore costly. The census trend cannot apportion shares among these causes, and this article does not try. What can be said, and what the record supports, is that the sharpest measured change in the mechanism the statute directly polices, the fall of overt refusal from common to rare in the testing series, coincides with the decades of steepest census decline. That coincidence is not proof, but it is the channel through which the statute most plausibly acted, and it is stronger than the correlation alone.

Where segregation held its ground

The national decline averages together places that desegregated and places that barely moved, and the places that barely moved cluster in the older industrial belt. John Logan and Brian Stults, in their 2011 report for the US2010 Project at Brown University and the Russell Sage Foundation, The Persistence of Segregation in the Metropolis: New Findings from the 2010 Census, measured the metropolitan areas where black-white dissimilarity stayed in the high 70s through 2010. The figures they reported: New York 79.1, Detroit 79.6, Newark 78.0, Milwaukee 79.6, Chicago 75.9 and Gary 76.8. The report explicitly named Cleveland and St. Louis as additional members of this group. On the Massey and Denton thresholds, where anything above 60 counts as high and anything above 75 as extreme, these metropolitan areas sat in the extreme band four decades after the Fair Housing Act’s passage, and the label the authors used for them, the Ghetto Belt, carried the implication that the pattern was structural rather than incidental.

The geography is not random. These are the metropolitan areas where the Great Migration concentrated black settlement between the 1910s and the 1960s, where municipal boundaries hardened early, and where the postwar highway and mortgage regimes drew white households to suburbs that then defended their borders with zoning. The statute banned the transactional discrimination that had helped build the pattern, but it did not redraw municipal lines, did not rewrite zoning codes, and did not redistribute the accumulated home equity that let one generation buy into appreciating suburbs while another could not. The result is visible in the contrast the two studies make when read together: Glaeser and Vigdor’s national average fell to 55, while Logan and Stults’s industrial metros held in the high 70s. A reader who cites only the national number understates what the statute left untouched; a reader who cites only the Ghetto Belt understates what changed. The complete guide to the 1968 act’s provisions explains why the transactional focus of the law maps cleanly onto individual acts of refusal and poorly onto metropolitan structure, and the pairing of the two measures is the article’s answer to the one test: segregation declined substantially, and high segregation persisted where the twentieth century had built it deepest.

There is a further measurement caution that belongs here rather than in a footnote. The dissimilarity index compares distributions within a metropolitan area, so a metro can hold a high score while the national average falls, and two metros with the same score can house very different lived experiences depending on the size of the minority population and the shape of the boundaries. The Logan and Stults figures are the most careful available snapshot of where separation stayed most rigid, and they cover the 2010 census, the most recent decennial administration within this article’s horizon. Nothing in the record suggests the reader should treat 2010 as a floor; it is a dated measurement, reported with its source and its year, and the next section shows why a single-group story was already incomplete by the time it was taken.

The mechanism that held these metros in place is the one the statute was never designed to dismantle. The Fair Housing Act polices transactions: the rental showing, the sale, the loan application. It does not reach the municipal fragmentation that lets a metropolitan area contain dozens of independent suburbs, each with its own zoning code, each free to require large lots and ban apartments, each thereby setting an income floor that functions as a racial filter without ever naming race. Exclusionary zoning of this kind was precisely what the Westchester litigation later attacked through the affirmatively-furthering duty, but as a nationwide phenomenon it lay beyond the transactional enforcement the testing studies could measure. A suburb that zones out every form of housing a working-class family can afford commits no discrete act of refusal for a tester to record; the exclusion happens in the ordinance, years before any homeseeker arrives. The Ghetto Belt’s persistence is in this sense the predictable residue of a law aimed at the point of sale operating in a landscape where the decisive choices were made at the drafting of the zoning map.

The contrast between the two scales is the article’s central empirical discipline. Quote the national 55 without the metro 79s and the statute looks more transformative than it was; quote the 79s without the national 55 and the statute looks futile, which the testing series disproves. Logan and Stults gave the field the dated, sourced, metro-level numbers that make the honest version possible, and their 2011 report remains the most recent decennial-based snapshot inside this article’s horizon. The reader should treat 2010 as a measurement with a date, not as a floor or a verdict, and should expect that the forces holding those metros in place, municipal boundaries, zoning, and the geography of accumulated equity, move on timescales far longer than the enforcement cycle of any single administration.

Hispanic and Asian patterns moved differently

The black-white decline is only one dimension of a record that grew more complicated as the country’s population changed. John Iceland, Daniel Weinberg and Erika Steinmetz, in a Census Bureau working paper presented to the Population Association of America in 2002, Racial and Ethnic Residential Segregation in the United States: 1980 to 2000, found that black segregation declined across all five standard dimensions of segregation between 1980 and 2000, while segregation of Asians and Pacific Islanders and of Hispanics tended to rise over the same span, with the larger increases belonging to Asians. The growth of those populations through immigration and natural increase meant that separation involving Hispanic and Asian residents was rising in the same decades that black-white separation was falling, and the aggregate American story became decline in one dimension alongside increase in others.

The decade that followed sharpened the distinction the earlier paper had drawn. Logan and Stults, in the same 2011 report that measured the Ghetto Belt, found that Asian-white dissimilarity rose from 42.1 in 2000 to 45.9 in 2010, while Hispanic-white dissimilarity was roughly flat, moving from 51.6 to 50.0. The responsible summary is therefore more precise than the familiar shorthand. Hispanic segregation rose through the late twentieth century as the Hispanic population grew rapidly and then flattened in the 2000 to 2010 decade; Asian segregation rose across both periods and was still rising in 2010. A reader who says separation involving Hispanic and Asian populations rose over the same period has the Asian half right and the Hispanic half overstated for the final decade. The distinction matters because the two groups arrived through different channels, settled in different metropolitan structures, and faced different forms of exclusion, and a statute evaluated on a single black-white axis will mislead a reader trying to understand what American neighborhoods actually looked like by 2010.

The multi-group record also complicates the isolation story in a way the dissimilarity trend alone hides. A group whose numbers grow rapidly can show rising isolation even as its dissimilarity falls or holds steady, because the isolation index depends on the group’s share of the metropolitan population. Hispanic population growth through the 1990s and 2000s meant that many Hispanic residents experienced neighborhoods that felt more separated even where the dissimilarity measure was flat, and the EPI critique of the Glaeser and Vigdor report made exactly this point about the limits of reading dissimilarity as lived experience. The article’s position is the one the sources support: the Fair Housing Act’s enforcement era coincided with a measurable decline in black-white dissimilarity, with rising then flattening Hispanic-white separation, and with rising Asian-white separation, and no single number captures the three together.

Immigration is the engine behind the multi-group complication, and the timing matters. The Hispanic and Asian populations grew rapidly through the last quarter of the twentieth century, driven substantially by immigration, and new arrivals tend to settle near earlier arrivals, in gateway neighborhoods where language, services and networks concentrate. That settlement logic raises measured separation even in the absence of any discriminatory act: a growing group clustering by choice in enclave neighborhoods will show rising dissimilarity and rising isolation on the standard indices. The Iceland, Weinberg and Steinmetz result, increases for Asians, Pacific Islanders and Hispanics across the five dimensions from 1980 to 2000, therefore cannot be read as a simple story of exclusion. It mixes voluntary clustering, the economics of new arrival, and the discrimination the testing studies separately document for Hispanic and Asian homeseekers. The field’s careful writers distinguish the components; the careless ones quote the trend as if it measured only bias.

The isolation dynamic sharpens the point. When a group’s metropolitan population share grows rapidly, its isolation index can rise even while its dissimilarity falls or holds flat, because the probability of same-group contact depends on how many same-group neighbors exist to be encountered. Hispanic population growth through the 1990s and 2000s meant that many Hispanic residents experienced neighborhoods that felt more separated in daily life at the same time the dissimilarity measure for 2000 to 2010 was essentially flat at 51.6 to 50.0. The Asian trajectory, 42.1 to 45.9 on dissimilarity over the same decade, shows the other pattern: rising evenness-separation alongside growth. Neither pattern is reducible to the black-white story, and a statute whose enforcement history was written overwhelmingly around black-white testing, the 1977 survey tested black and white homeseekers only, and Asian testers did not enter the federal series until 2012, was always going to be an imperfect instrument for understanding them. The honest summary remains: decline in one dimension, increase in others, with the Hispanic increase concentrated before 2000 and the Asian increase continuing through 2010.

Ownership: the rate that did not move and the gap that grew

The homeownership record is the section of this article where precision is not a virtue but the entire point, because the most quoted statistic in the field is routinely misstated. The exact source for the frequently repeated claim that the black homeownership rate was 41.1 percent in 1968 and 41.2 percent in 2016 is post-horizon for this article: the figure pair comes from the Economic Policy Institute’s 2018 fiftieth-anniversary analysis and the Urban Institute’s February 2017 writing, both published after this article’s February 1, 2016 reference date, and this article does not use them. The in-horizon grounding, all of it published on or before the reference date, is as follows. The series is the Census Bureau’s Current Population Survey and Housing Vacancy Survey, the CPS/HVS, whose historical table reports the homeownership rate by race of householder on a quarterly and annual basis, supplemented for the early year by the 1970 decennial census. William Collins and Robert Margo, in their 2001 paper Race and Home Ownership in Twentieth Century America, report the 1970 census black homeownership rate at 42.1 percent against a white rate of 66.8 percent, a white-black gap of roughly 25 percentage points. The Housing Vacancy Survey for the fourth quarter of 2015, released in January 2016 and therefore inside the horizon, put the black homeownership rate at 41.5 percent in contemporary reporting, with the series running 41.5 to 41.9 percent for the year, against a non-Hispanic white rate of 72.1 percent, a gap of roughly 30 percentage points.

Set beside each other, the two moments say something sharper than any slogan. The black rate was near 42 percent in 1970 and near 42 percent in 2015: effectively flat across forty-five years. The white rate moved from 66.8 percent to 72.1 percent over the same span. The gap therefore did not stand still; it widened from roughly 25 points to roughly 30 points. Any telling that says the gap stands where it stood at enactment has confused the rate with the gap. The rate is flat. The gap grew by about five percentage points. A reader who repeats the confused version in public will be corrected by anyone who has done the arithmetic, and an impact article cannot afford to be the source of the confusion.

The flat line also hides a rise and a fall that the annual series makes visible. The black homeownership rate did not sit at 42 percent for the whole period; it climbed through the 1990s and early 2000s, peaking at 49.1 percent in 2004, before the foreclosure crisis erased every point of the gain and returned the rate to its 1970 level by 2015. That boom-bust arc is why the horizon’s endpoint looks like stasis while the lived experience of the period was anything but. The gains of the 1990s and early 2000s were real, they were measured in the same CPS/HVS series that measures the endpoint, and they were wiped out in the crisis years by a wave of foreclosures that fell disproportionately on black homeowners, many of whom had been steered into subprime products they could have avoided, a pattern the lending section documents with the settlement record. A reader who knows only the endpoints misses the mechanism; a reader who knows only the peak misses the outcome.

The comparison also requires a series discipline that the literature enforces and casual commentary often ignores. The 1970 figure comes from the decennial census and the 2015 figure from the Housing Vacancy Survey, and the two series define the householder and the housing unit consistently enough for the comparison to be standard practice: Collins and Margo’s 42.1 percent is the 1970 census figure the field uses, and the HVS fourth-quarter 2015 release is the in-horizon endpoint. Comparing a decennial census number to a survey number from a different decade without naming both series is the recurring error the brief warned against, and it is why this section names the series, the years and the measure for every figure. The takeaway survives the discipline intact: measured on a consistent series basis, black homeownership ended the period where it began, and the white-black gap was about five points wider at the end than at the start.

The longer historical arc makes the flat line more intelligible. Collins and Margo’s 2001 paper, Race and Home Ownership in Twentieth Century America, traces black homeownership across the full century, and the 1970 figure of 42.1 percent that anchors this article’s comparison sits inside that longer series. The rate rose substantially across the twentieth century’s middle decades, which means the flat line from 1970 to 2015 is not a century of stasis but a half-century in which the earlier gains stopped compounding. The white rate’s move from 66.8 to 72.1 percent over the same span is what opened the gap, and it reflects the continued accumulation of the advantages the earlier decades had distributed: suburban homes bought when credit was cheap and discrimination was legal, appreciating across the decades, their equity financing the next generation’s down payments. The gap is in this sense a stock measure wearing a flow measure’s clothes. It records at a point in time the accumulated result of decades of differential access to the asset, not merely the discrimination operating in the year of measurement.

The measurement note on the white series deserves a sentence, because careful readers will ask why the 2015 white figure is reported for non-Hispanic whites. The Census Bureau’s Housing Vacancy Survey reports homeownership by race and by Hispanic origin separately, and the white series that the field compares against the black series is conventionally the non-Hispanic white rate, 72.1 percent in the fourth quarter of 2015, to avoid mixing the Hispanic homeownership experience into the white baseline. Using the all-white rate instead would change the gap by a small amount without changing its direction or its approximate size, and the article follows the field’s convention while naming it. The black series is reported for black householders without the Hispanic-origin split in the figures used here, which is the standard presentation in the historical table.

The rise to 49.1 percent in 2004 and the fall back to 42 percent by 2015 complete the picture, and they connect the ownership section to the lending section that follows. The gains of the 1990s and early 2000s coincided with a historic expansion of mortgage credit, including the subprime products that the post-crisis settlements would later document as disproportionately sold to black borrowers on disadvantageous terms. Ownership bought with a subprime loan at the peak of a bubble is ownership in name; when prices fell, the equity vanished first and the foreclosure followed, and the CPS/HVS series recorded the erasure year by year until the rate stood where it had stood in 1970. A reader who treats the flat line as evidence that nothing happened between 1970 and 2015 misses the boom, the bust, and the mechanism that connected them. A reader who treats the 2004 peak as the true measure of progress misses the terms on which it was built.

How can the rate stand still while the gap widened?

Because the two numbers measure different things. The black rate compares black homeowners to black households across years; the gap compares black and white rates within each year. White homeownership rose from 66.8 to 72.1 percent while the black rate held near 42, so the distance between the lines grew while the lower line stayed level.

Why the Rate-versus-Gap Distinction Changes the Argument

The verification memo’s central correction, that the black rate stood still while the gap widened, is worth dwelling on, because the two framings support different arguments and only one of them is true. The false framing, that the gap stands where it stood at enactment, implies a statute that changed nothing, a flat line against a flat line. It invites the conclusion that the Fair Housing Act failed outright, and it is the version that circulates most widely in public discussion. The true framing, a flat black rate against a rising white rate producing a widening gap, implies something more specific and more damning in its own way. It says the statute’s beneficiaries, defined broadly as the market the act opened, advanced, while black households did not, and that the relative position of black households deteriorated even as absolute exclusion declined. The first framing describes stagnation. The second describes falling behind.

The distinction matters for the same reason the article distinguishes the statute’s aims from projected aims. A defender of the statute can answer the false framing by pointing to the testing studies, the segregation decline, and the enforcement record, and the defense has force, because the gap-did-not-move claim is factually wrong about the gap and silent about everything the statute did change. The true framing is harder to answer, because it concedes the transaction evidence and still finds the distributional outcome unacceptable. The article’s position is that the true framing is the one the evidence supports, and that the statute’s defenders should argue from it rather than from the false version. Access improved and ownership did not is a concession wrapped in a claim. The concession is the ownership record. The claim is that a transaction statute was never the instrument for closing a wealth gap, and that the gap’s widening indicts the broader political economy of housing wealth rather than the enforcement of the transaction bans.

The peak-and-erasure detail sharpens the true framing further. The black rate did not merely sit at forty-two percent. It rose to 49.1 percent in 2004 and then surrendered the gains, which means black households experienced the boom as renters-becoming-owners and the bust as owners-becoming-renters, while white households experienced the same cycle with less amplitude. The asymmetry is the wealth mechanism in miniature. Leverage without cushion produces ownership that the first serious shock repossesses. The article presents the arc without flinching because the one test requires it. A reader who can state the rate, the gap, the peak, and the erasure, with the series and years for each, has the ownership finding in full, and no simpler version survives the numbers.

Finding Three: Four Decades of Paired Tests

The strongest causal evidence in fair housing comes from a method whose logic a reader can grasp in one sentence. Two testers, matched on every characteristic except the one being tested, inquire about the same advertised units in the same order, and the researcher records whether they are told about the same units, shown the same units, quoted the same terms, and steered to the same neighborhoods. Because the testers are matched, differences in treatment can be attributed to the characteristic that differs. The federal government has run this method at national scale four times, and the four studies form the backbone of everything known about the incidence of housing discrimination as distinct from the volume of complaints about it. Complaints measure the willingness and ability to complain. Paired tests measure what happens at the counter.

The first study was the Housing Market Practices Survey, with fieldwork in 1977 and a report published in 1979 by Ronald Wienk, Clifford Reid, John Simonson, and Frederick Eggers for HUD, titled Measuring Racial Discrimination in Housing Markets. The survey conducted about three thousand two hundred sixty-four tests in forty metropolitan statistical areas, testing black and white homeseekers only. Its finding, summarized by Seok Joo Oh and John Yinger in their 2015 Cityscape review, was that overt refusal was common: about one in three black renters and about one in five black homebuyers were told that nothing was available. The 1977 study therefore captures the market as it operated less than a decade after the 1968 act, before the 1988 amendments, and its numbers describe a world in which crude exclusion was routine.

Why the 1977 Baseline Matters

The Housing Market Practices Survey’s 1977 fieldwork occupies a specific historical position that gives it unusual evidentiary value. It measured the market nine years after the 1968 act and one year before the 1988 amendments, which means it captures what the original statute achieved on its own, without the administrative enforcement machinery the amendments later added. The answer, about one in three black renters and one in five black homebuyers told nothing was available, is the measure of the original act’s limits. The prohibitions were on the books. The crude exclusion continued. The comparison with the 1989 study, fielded just as the amendments took effect, is therefore the closest the federal series comes to a before-and-after test of the enforcement upgrade, and its result, overall discrimination against black homeseekers essentially unchanged since 1977 but subtler in form, suggests the original act moved discrimination’s form more than its incidence.

The 1977 study’s design also reflects the market it measured. With about three thousand two hundred sixty-four tests in forty metropolitan statistical areas and black and white testers only, it was built for a black-white housing market in which overt refusal was the modal form of discrimination. Its finding that refusal was routine is consistent with the testing organizations’ field reports from the period and with the private litigation record, in which testers documented landlords and agents simply declining to engage. The study’s limitation, that it could not measure the subtler forms the later studies found, is a limitation of its era rather than its authors. In 1977, the subtle forms were not the binding constraint. The door was closed. Measuring how far it was ajar could wait until it opened.

The baseline matters finally because it disciplines the optimistic reading of the later decline. When the 2012 study found overt refusal rare, the comparison that gives the finding meaning is the 1977 world in which refusal was common. Without the baseline, the 2012 differentials, 11.4 percent fewer units told about, 4.2 percent fewer shown, could read as evidence of a mildly imperfect market. Against the baseline, they read as the residue of a transformation, the portion of the old exclusion that survived its change of form. The article’s verdict on detected discrimination, overt refusal fell sharply while subtler shortfalls persisted, is a two-part claim that requires both endpoints, and the 1977 survey supplies the first.

The second study is the one the brief misdated, and the correction is binding. The Housing Discrimination Study of 1989, HDS1989, conducted its fieldwork in the spring and summer of 1989 and published its reports in 1991, including the synthesis volume by Margery Turner, Raymond Struyk, and John Yinger, Housing Discrimination Study: Synthesis, published by HUD in September 1991, with companion volumes on incidence and severity, on racial and ethnic steering, and on methodology. The study conducted about three thousand eight hundred audits in twenty-five metropolitan areas and tested black and Hispanic homeseekers. Its headline result was double-edged. Overall discrimination against black homeseekers was essentially unchanged since 1977, but its forms had grown more subtle. Black and Hispanic testers were shown about twenty-five percent fewer units than their white teammates. The refusal had become the shortfall. The door was no longer slammed. Fewer rooms were shown on the other side of it.

The third study, the Housing Discrimination Study of 2000, conducted fieldwork in 2000 and 2001 and published its results in 2002 and 2003, with the national Phase I results by Turner, Ross, Galster, and Yinger appearing as Discrimination in Metropolitan Housing Markets in 2002 and the Phase 2 and 3 results by Turner and Ross in 2003. HDS2000 found that discrimination against black homeseekers declined between 1989 and 2000 in both rental and sales markets, that discrimination against Hispanic homebuyers also declined, and that discrimination against Hispanic renters showed no change. This is the study that most clearly captures the effect of the 1988 enforcement regime operating at maturity, and its direction is the most favorable in the series.

The fourth study, the Housing Discrimination Study of 2012, conducted fieldwork in 2011 and 2012 and was published in June 2013 by Turner and colleagues as Housing Discrimination Against Racial and Ethnic Minorities 2012, produced with the Urban Institute for HUD. It was the largest of the four, with more than eight thousand tests in twenty-eight metropolitan areas, and it tested Asian homeseekers alongside black and Hispanic homeseekers. Its findings describe a market in which overt refusal had become rare and subtler differences persisted in measurable form. Black renters were told about 11.4 percent fewer units and shown 4.2 percent fewer units than white renters. Hispanic renters were told about 12.5 percent fewer and shown 7.5 percent fewer. Asian renters were told about 9.8 percent fewer and shown 6.6 percent fewer. Black homebuyers were told about seventeen percent fewer homes and shown about eighteen percent fewer than white homebuyers. The pattern across the four studies is therefore consistent in direction. Crude exclusion fell sharply. Differential treatment in the number of units mentioned and shown persisted at levels that are small in any single transaction and large in the aggregate, because a homeseeker who is shown fewer units in every search accumulates a thinner choice set over a lifetime of searches.

The methodology carries a stated limit that the article honors rather than buries. The four studies differ in sample design, in the metropolitan areas covered, in the groups tested, and in the measures reported, and the study authors state explicitly that these differences prevent precise trend comparisons across the four studies. Only qualitative trends can be drawn. The article therefore does not present a single clean time series of discrimination. It presents four snapshots taken with four cameras and describes the direction in which the picture moved. A reader who wants a precise annual trend in discrimination will not find one here, because the federal government never built the instrument that would produce it.

What the 2012 Study Added: New Groups and New Measures

The Housing Discrimination Study of 2012 expanded the federal testing program in two ways that matter to the article’s evidence. First, it added Asian homeseekers as a tested group alongside black and Hispanic homeseekers, producing the first national paired-testing estimates for Asian Americans. The findings showed Asian renters told about 9.8 percent fewer units and shown 6.6 percent fewer than white renters, differentials smaller than those measured for black and Hispanic testers but statistically distinguishable from zero. The inclusion matters because the Asian population’s growth had made its absence from the earlier studies an increasingly visible gap, and because the results showed that subtle differential treatment was not confined to the black-white axis the 1977 survey had measured.

Second, the 2012 study measured more stages of the search process than its predecessors, recording not only whether units were mentioned and shown but also the number of units involved, the follow-up contact testers received, and the geographic distribution of shown homes. The headline figures, black renters told about 11.4 percent fewer units and shown 4.2 percent fewer, black homebuyers told about seventeen percent fewer homes and shown about eighteen percent fewer, describe the intensive margin of discrimination, how much less minority testers received, rather than the extensive margin, whether they received anything at all. The shift from extensive to intensive measurement is itself a finding about the market’s evolution. In 1977, the question was whether the door opened. In 2012, the question was how wide.

The study’s scale, more than eight thousand tests in twenty-eight metropolitan areas, made it the most statistically powerful of the four, and its June 2013 publication date places it firmly inside the article’s horizon. Its authors stated the cross-study comparability limit explicitly, and the article honors it. What the 2012 study establishes on its own is that subtle differential treatment persisted at measurable levels a full generation after the 1988 amendments, in a market where overt refusal had become rare. That is the finding the article’s third row summarizes, and it is the evidence the complaint record cannot supply.

How Paired Testing Works and Where It Stops

The paired test is simple in concept and demanding in execution. A testing organization recruits and trains testers who are matched on age, sex, dress, demeanor, family composition, and every other characteristic the landlord or agent might notice, except the characteristic being tested. The testers inquire about the same advertised units, usually within hours of each other, following a script that standardizes the questions they ask and the information they volunteer. After each visit, the tester completes a detailed report form recording which units were mentioned, which were shown, what terms were quoted, what fees were named, and whether the tester was steered toward or away from particular neighborhoods. The organization then compares the paired reports. Because the testers were matched, systematic differences across many tests can be attributed to the characteristic that differed. A single test proves little. Hundreds of tests prove a pattern.

The method’s strength is that it measures behavior at the point of transaction, which is exactly what the statute regulates. Its limits are worth stating because they bound what the four federal studies can claim. First, testing captures the search process, not the outcome. A tester who is shown fewer units may still find housing, and the studies do not measure the ultimate housing quality the tester obtains. Second, testing is expensive, which is why the federal studies occur roughly once a decade rather than annually, and why the article cannot offer a yearly trend. Third, the studies test the markets and groups their funders choose. The 1977 survey tested black and white homeseekers only. Hispanic testers entered in 1989. Asian testers entered in 2012. Discrimination against other groups, or in rural markets the studies do not cover, goes unmeasured. Fourth, the method detects differential treatment, not motive. A landlord who shows fewer units to black testers may act from animus, from statistical stereotyping, or from deference to the perceived preferences of white tenants. The statute reaches all three, but the remedy and the moral judgment differ.

The steering finding deserves separate attention because it is the subtlest form the studies document and the hardest to remedy. Steering occurs when an agent shows minority homeseekers homes in minority neighborhoods and white homeseekers homes in white neighborhoods, preserving segregation without ever refusing anyone. The 1989 study’s companion volume on steering documented the practice, and the 2012 study’s neighborhood-level analysis found its traces in the geographic distribution of shown units. Steering is invisible to the steered homeseeker, who sees only the homes shown, and it is the mechanism through which the segregation finding and the testing finding connect. The dissimilarity index measures where people live. Steering measures one of the processes that puts them there. The decline in overt refusal alongside the persistence of differential showing is consistent with a market in which steering replaced refusal as the primary sorting mechanism, though the studies’ methodological differences prevent a precise quantification of that substitution.

Steering: The Sorting Mechanism That Replaced Refusal

Steering is the practice the later testing studies were built to detect, and it is worth understanding in detail because it explains how segregation persists without refusals. In its classic form, a real estate agent shows black homebuyers homes in black or integrating neighborhoods and white homebuyers homes in white neighborhoods, matching the buyer to the agent’s expectation of where each belongs. No one is told nothing is available. Everyone is shown something. But the choice sets differ by race, and the cumulative effect across thousands of transactions is the maintenance of the dissimilarity the census measures. The 1989 study’s steering companion volume documented the practice systematically, and the 2012 study’s geographic analysis of shown units found its continued traces.

Steering is difficult to prove in an individual case, which is why the testing method matters. A single homebuyer cannot know which homes the agent showed to the last buyer. A testing organization running hundreds of paired tests can compare the racial composition of the neighborhoods where black testers were shown homes against those where white testers were shown homes and test whether the difference exceeds chance. The federal studies did exactly this, and their steering findings are among the most policy-relevant in the series, because steering operates through the discretion of intermediaries rather than through the decisions of owners. The statute reaches intermediaries explicitly, banning discriminatory brokerage services, but enforcement requires the testing infrastructure to generate the evidence.

The relationship between steering and the segregation finding runs in both directions. Steering maintains segregation, and segregation enables steering, because an agent who assumes buyers prefer same-race neighborhoods can point to the existing pattern as justification. Breaking the cycle requires either changing the pattern or policing the assumption, and the statute attempts the second while hoping for the first. The measured decline in dissimilarity suggests the cycle weakened. The persistence of high-seventies readings in the older industrial metros suggests it did not break. The article presents steering as the mechanism connecting the transaction evidence to the geographic evidence, and as the reason the testing finding’s subtle differentials matter out of proportion to their size in any single search.

The article’s rating of the testing finding, measurable within studies with only qualitative trends across them, reflects these limits honestly. The four studies are the strongest causal evidence available, and they are strong enough to support the article’s central descriptive claims. They are not strong enough to support a precise annual time series of discrimination, and the article does not pretend otherwise. A reader who encounters a claim that discrimination fell by a specific percentage between two specific years should ask which study measured both years with the same method. The answer, in every case the article could verify, is that none did.

The testing evidence also explains a feature of the enforcement record that otherwise puzzles readers. Private fair housing organizations conduct the large majority of paired tests and file or support the large majority of complaints, which means the enforcement system depends on a private testing infrastructure that the federal studies validate but do not fund at scale. The testers who can sue under the statute, a standing question the Supreme Court resolved in favor of tester standing decades ago, are the enforcement mechanism the 1968 Congress built without quite naming. The doctrine that shapes what those suits can prove, including the intent and effects frameworks, is covered in the companion article on Supreme Court cases, and the article does not duplicate that coverage here.

Why do complaint counts understate discrimination?

Complaint counts understate discrimination because most victims never learn it happened. A homeseeker shown fewer units cannot know what the white tester was shown, so the injury stays invisible. Paired testing exists precisely to reveal what the complaint record cannot see on its own.

Finding Four: The Complaint Record and Its Disability Majority

The fact that surprises nearly every reader of the enforcement record is that the large majority of fair housing complaints filed each year concern disability rather than race. The in-horizon source is the National Fair Housing Alliance’s Fair Housing Trends Report, 2015 edition, published in April 2015 and covering calendar year 2014. The report counted 14,272 instances of disability-based discrimination, 51.8 percent of all complaints nationwide, with race second at 22.0 percent, or 6,044 instances. Within the HUD-only portion of the data, the disability share was 53.2 percent. The article cites the 2015 edition and its 2014 data rather than the 2016 edition, whose 2015 data showed a disability share of 55.1 percent but which was published in April 2016, after the article’s reference date. Corroboration comes from HUD’s own Research Works publication, volume 6 number 7 in 2009, which reported that the majority, forty-two percent, of complaints from 2005 through 2008 were disability-based, and from the Congressional Research Service’s report R44557, which notes that disability has been the largest single basis of complaints since fiscal year 2005. The CRS figure for fiscal year 2019, sixty-two percent, is outside the horizon and is not cited as a finding.

The disability majority follows directly from the 1988 amendments, and the article presents the mechanism rather than treating the number as a mystery. The 1988 amendments added disability and familial status as protected classes and, crucially, created duties whose violation is visible to the person affected. A landlord who refuses to permit a reasonable accommodation, such as an assistance animal in a no-pets building or a reserved accessible parking space, commits a violation the tenant can see. A landlord who shows a black homeseeker fewer units commits a violation the homeseeker cannot see without a paired tester. Visible violations generate complaints. Invisible violations generate tests. The complaint mix therefore describes the enforcement system’s intake, not the incidence of discrimination in the market, and the paired testing finding is the necessary companion to the complaint finding. Each corrects the other.

Three caveats travel with the numbers. First, the National Fair Housing Alliance aggregates complaints processed by private fair housing organizations, by state and local agencies in the Fair Housing Assistance Program, by HUD, and by the Justice Department, and these are different intake systems with different reporting practices. Second, HUD cautions that a single case may allege multiple bases of discrimination, so the percentages by basis can sum to more than one hundred percent, and the 51.8 and 22.0 percent figures should be read as shares of alleged bases rather than as a partition of cases into mutually exclusive bins. Third, private fair housing organizations process the large majority of complaints, which means the national total is substantially a record of private enforcement activity rather than of federal intake alone. A reader who treats the complaint total as a measure of how much discrimination occurs is making the category error the article’s third finding exists to prevent. The complaint record measures the visible portion. The testing record measures the portion that testing can reveal. Neither measures the whole.

The finding’s rating is settled as to the mix and measurable as to the trend. The disability share has been the largest since fiscal year 2005 on the CRS accounting, and nothing in the in-horizon record suggests the ordering changed. What the mix means for the statute’s success is contested in the advocacy literature, with disability organizations reading it as evidence that the 1988 amendments worked as designed and race-focused organizations reading it as evidence that race discrimination has gone underground into forms the complaint system cannot catch. The article reports the numbers with their source and leaves the inference to the reader, with the testing evidence supplied as the relevant context.

The Complaint Pipeline, Step by Step

A complaint’s journey through the enforcement system explains why the national totals look the way they do. A person who believes they experienced housing discrimination may file with HUD within one year of the alleged act, may file with a state or local Fair Housing Assistance Program agency where one exists, or may contact a private fair housing organization, which may test the allegation, counsel the complainant, and help file. HUD refers complaints to FHAP agencies in jurisdictions with substantially equivalent laws, which means a large share of nominally federal complaints are actually investigated by state and local agencies under work-sharing agreements. Private organizations, funded in part through HUD’s Fair Housing Initiatives Program, conduct the testing and outreach that generate many of the complaints they then help file. The 27,528 complaints the Alliance counted for 2014 are therefore the output of a hybrid public-private pipeline, and the private organizations’ testing capacity is the binding constraint on how much hidden discrimination the pipeline can surface.

Once filed with HUD, a complaint enters investigation. HUD investigators gather documents, interview witnesses, and may conduct or commission testing. If the investigation finds reasonable cause to believe discrimination occurred, HUD issues a charge, and the case proceeds either before a HUD administrative law judge or, at the election of any party, to federal court. The administrative law judge can award actual damages to the aggrieved person, impose civil penalties payable to the government, and order injunctive relief. If conciliation succeeds at any stage, the case closes with an agreement. The Justice Department enters through a separate door, bringing pattern or practice suits and cases of general public importance, which is the authority behind the Countrywide and Wells Fargo settlements. The department can also intervene in private suits. The pipeline’s design reflects the 1988 compromise: administrative efficiency for individual cases, federal litigation muscle for systemic ones.

The disability majority looks different once the pipeline is understood. Reasonable accommodation requests arrive as correspondence, a tenant’s letter requesting an assistance animal, a doctor’s note requesting a parking accommodation, and the denial arrives as correspondence too. The paper trail makes investigation straightforward and the violation legible to the complainant, the investigator, and the adjudicator alike. A steering claim, by contrast, requires paired tests the complainant cannot perform alone, statistical analysis of showing patterns, and an investigator willing to pursue a case built on inference rather than documents. The pipeline processes what it can see efficiently and what it cannot see with difficulty, and the complaint mix is the predictable result. The article’s point is not that the pipeline is broken. It is that the pipeline measures its own intake, and intake is not incidence.

The Justice Department’s authority in this field comes in two forms, and the settlements illustrate the stronger one. The Department may sue on behalf of an individual complainant whose case HUD refers after investigation, and it may bring its own pattern-or-practice actions alleging that a lender or other housing provider engaged in a systematic course of discrimination. The Countrywide and Wells Fargo settlements were pattern-or-practice resolutions, built on statistical analyses of hundreds of thousands of loans rather than on individual complaints, and they show what the 1988 amendments’ strengthened litigation authority was for. A complaint-driven system waits for victims who can see the violation; a pattern-or-practice system goes looking for the violations the victims cannot see, using the disclosure data and the testing evidence as its map. The two largest fair lending settlements in the country’s history at the time were therefore not accidents of the crisis but the predictable output of an enforcement design that paired disclosure with the power to act on what disclosure revealed.

The Reasonable Accommodation Duty in Practice

The reasonable accommodation duty is the engine of the disability complaint majority, and its mechanics explain both the volume and the visibility. The duty requires housing providers to make exceptions to rules, policies, and procedures when necessary for a person with a disability to use and enjoy the dwelling. The classic cases involve assistance animals in no-pet buildings, reserved accessible parking spaces near unit entrances, and permission for a live-in aide despite occupancy limits. The request typically arrives in writing, often with medical documentation, and the denial arrives in writing too. The resulting paper trail gives investigators a clean factual record and gives adjudicators a discrete decision to evaluate, which is why accommodation cases move through the pipeline more efficiently than steering cases built on statistical inference from paired tests.

The duty’s scope has been elaborated through HUD guidance and adjudication rather than through the testing studies, which is another reason the complaint record and the testing record diverge. Testing organizations rarely test accommodation requests, because the test would require presenting a disability the tester does not have, raising ethical and methodological questions the race tests do not. The enforcement of the accommodation duty therefore depends almost entirely on complaints, and the 51.8 percent disability share reflects a system working as designed for the violations it can see. The article notes this asymmetry because it bears directly on the one test. A reader who asks what measurably changed since 1968 must understand that the complaint mix measures the 1988 duties well and the 1968 duties poorly, and that the testing studies exist to fill exactly that gap.

The familial status and disability provisions together show the 1988 amendments’ distinctive contribution. The original act banned exclusions. The amendments added affirmative duties, to accommodate, to permit modifications, to accept children, whose breach is observable. The enforcement record’s shape, a disability majority built on visible violations alongside a testing record documenting invisible ones, is the predictable output of that two-part design. Neither record alone describes the statute’s effects. Together they describe a system that catches what it can see and needs testers for the rest.

Reading the 2014 Tables: What the Complaint Numbers Contain

The National Fair Housing Alliance’s 2015 Trends Report, the article’s in-horizon source for the complaint mix, is worth understanding as a document, because its construction shapes what the numbers mean. The Alliance collects complaint data from its member private fair housing organizations, from state and local agencies participating in the Fair Housing Assistance Program, from HUD’s own intake, and from the Justice Department, and it publishes the aggregate as the national total. The 2014 total of 27,528 complaints is therefore a composite of systems with different definitions, different reporting practices, and different thresholds for recording a contact as a complaint. A person who calls a private organization for advice may be counted differently than a person who files a formal HUD charge, and the Alliance’s methodology notes acknowledge the resulting imperfections. The article uses the published totals because they are the standard national series, not because they are precise.

The basis breakdown within the total carries the same composite character. The 14,272 disability instances and 6,044 race instances are counts of alleged bases, and HUD’s caution that one case may allege multiple bases means the 51.8 and 22.0 percent shares describe allegations rather than cases. A complaint alleging both race and disability discrimination appears in both counts. The ordering, disability first and race second, is robust to this caveat, because the disability margin is large enough that no plausible reallocation of multi-basis cases would reverse it. The corroborating sources strengthen the reading. HUD’s Research Works found a disability plurality for 2005 through 2008, and the Congressional Research Service’s R44557 places disability as the largest single basis since fiscal year 2005. Three different tabulations across overlapping periods agree on the ordering, which is why the article rates the mix as settled.

The report also distinguishes new complaints from the stock of pending cases, a distinction the article honors by citing only the flow. Enforcement systems carry backlogs, and a snapshot of pending cases can reflect past filing surges rather than current intake. The 2014 flow figures describe what entered the system in that year, which is the right measure for the article’s question about what the enforcement record contains. The article does not report resolution rates, damages awarded, or conciliation outcomes, because those figures vary by forum and the Alliance’s national aggregation does not support clean comparisons. What the tables establish, and all the article claims for them, is the composition of intake: a disability majority, a race second, and a private-organization pipeline processing most of it.

Lending: raw gaps, adjusted gaps and the limits of both

The lending record is where the statute’s effects are hardest to isolate and easiest to misread, because the data that made discrimination visible also made it contestable. The Home Mortgage Disclosure Act required lenders to report loan applications and decisions by race, and the raw HMDA numbers showed denial gaps that were impossible to ignore and impossible, on their own, to interpret. The study that defined the field’s handling of this problem was conducted not nationally but in one metropolitan area, a limitation this article carries in every mention. Alicia Munnell and her coauthors at the Federal Reserve Bank of Boston, in Mortgage Lending in Boston: Interpreting HMDA Data, first circulated as a Bank working paper in 1992 and published in the American Economic Review in 1996, started from the raw 1990 HMDA figures for the Boston metropolitan statistical area: minority applicants were two to three times as likely to be denied a mortgage as white applicants, a raw ratio of roughly 2.7 to 1. The team then collected 38 additional variables from the lenders’ own loan files, covering the applicant’s financial position, the property, and the loan terms, and re-estimated the disparity with those controls in place. The adjusted ratio fell to roughly 1.6 to 1: black and Hispanic applicants were about 60 percent more likely to be turned down than similarly situated white applicants. The gap narrowed under scrutiny and did not vanish.

The study’s limits are as instructive as its findings, and the literature has never let them be forgotten. HMDA data omit credit history and other underwriting variables that lenders consider legitimate, and the industry’s standard criticism of the Boston study has always been that the missing variables, not discrimination, explain the residual gap. The study’s defenders answer that 38 controls is an unusually rich specification and that the persistence of a 60 percent disparity after controlling for the observable economics of the loan is difficult to square with a purely race-neutral process. The study was also confined to Boston, and its methods were contested in the economics literature, so it cannot be read as a national estimate. HUD’s own synthesis, What We Know About Mortgage Lending Discrimination in America, reported a parallel result from a basic model: the probability of denial ran about 80 percent higher for black and Hispanic applicants after controls for loan, property and applicant characteristics. The two results do not agree numerically, and the article does not force them to; they agree on the shape of the finding, which is the shape the field reports with the most confidence. Raw denial gaps overstate what can be attributed to discrimination because they omit underwriting variables; adjusted gaps still show disparities that the measured economics of the loans do not explain; and neither number by itself proves discrimination in any individual case.

What the post-crisis years added to this record was not a new study but a set of settlements large enough to function as findings about the market’s recent past. The Department of Justice announced on December 21, 2011 that Bank of America, as successor to Countrywide, would pay $335 million to resolve allegations that Countrywide had charged more than 200,000 black and Hispanic borrowers higher rates and fees than white borrowers, or steered them into subprime mortgages despite their qualifying for prime loans, in lending from 2004 through 2008. The Department’s press release called it the largest residential fair lending settlement in history, a characterization true as stated in 2011 and qualified here as at the time. The case was filed in the Central District of California and rested on the pattern-or-practice authority the statute gives the Department. Seven months later, on July 12, 2012, the Department announced a $175 million settlement with Wells Fargo, which it called the second largest settlement over fair lending violations, again qualified as at the time. The Wells Fargo settlement covered roughly 34,000 black and Hispanic borrowers in 36 states and the District of Columbia, loans originated from 2004 through 2009, with $125 million in borrower compensation and $50 million committed to a down-payment assistance program; the bank did not admit wrongdoing.

The settlements sit in the record as enforcement outcomes, not as controlled estimates, and the article treats them that way. They establish that the Department found patterns it was prepared to litigate as discrimination, that the patterns touched hundreds of thousands of borrowers in the case of Countrywide and tens of thousands in the case of Wells Fargo, and that the dollars attached were the largest the fair lending docket had produced to those dates. They do not establish a national denial rate, and they cover lending from the bubble years, which is why they belong to the story of how the homeownership gains of the early 2000s were built on terms that made the subsequent losses worse. The connection back to the homeownership section is direct: the same borrowers whose ownership the CPS/HVS series counted in the 2004 peak were disproportionately the borrowers the settlements describe, and the erasure of the gains by 2015 is the other side of the same ledger. A reader who wants the statute’s lending provisions in full, and the Community Reinvestment Act’s parallel record on credit access, follows the internal links this article has already given; the point here is the measured outcome, stated with its limits.

The debate over the Boston study never ended, and the article should give the reader its shape rather than its verdict. The study’s methods were contested in the economics literature on the ground that the 38 variables, extensive as they were, could not capture everything a lender legitimately considers, and that the residual 1.6-to-1 disparity reflected unmeasured creditworthiness rather than discrimination. Reworkings of the data in some hands produced smaller or statistically insignificant residual effects, and the exchange ran for years. The study’s defenders answered that the specification was unusually rich for the era, that the variables came from the lenders’ own files rather than from public records, and that a 60 percent residual disparity is a large effect to attribute entirely to the unmeasured. HUD’s synthesis, reporting an 80 percent higher denial probability after controls in its basic model, pointed in the same direction without settling the methodological fight. The field’s working consensus, to the extent one exists, is the shape both sides’ numbers share: controls shrink the raw gap substantially and leave a remainder that the measured economics do not explain. That remainder is evidence consistent with discrimination, not proof of it, and the article holds the line there.

The disclosure regime that made the debate possible deserves its own acknowledgment. The federal disclosure law required lenders to report applications, decisions and borrower characteristics, creating the first systematic public record of who got turned down and who did not. Without that record there would have been no raw ratios to argue about, no Boston study to contest, and no empirical basis for the pattern-or-practice cases that followed. Disclosure did not prove discrimination, but it made the question answerable, and the twenty-year argument over the answer is itself a measure of the statute’s informational footprint. The post-crisis settlements then supplied what statistical argument could not: named institutions, named practices, and dollar figures. Countrywide’s $335 million and Wells Fargo’s $175 million did not estimate a national disparity; they documented that in the bubble years, hundreds of thousands of minority borrowers paid more for credit than similarly qualified white borrowers, or were steered into products built to fail them. The settlements belong to the enforcement record and to the ownership record at once, because the borrowers they describe are the households whose foreclosures the homeownership series recorded on the way down from 49.1 percent.

HUD’s own synthesis of the lending literature, What We Know About Mortgage Lending Discrimination in America, gives the Boston result its closest corroboration and its clearest statement of the residual-gap finding. The synthesis reported that a basic model controlling for loan, property and applicant characteristics found the probability of denial roughly 80 percent higher for black and Hispanic applicants than for comparable white applicants. The figure differs numerically from the Boston study’s 60 percent, and the article does not reconcile them, because the two estimates come from different data, different specifications and different years. What they share is the shape: a raw gap that shrinks substantially under controls and a remainder that the measured variables do not explain. Presented together with the stated limits, the omitted credit history, the single-metropolitan-area scope, the contested methods, the two estimates bracket the field’s best quantitative answer to the question the disclosure law made askable. The honest version of the lending finding is a range with a caveat, not a point with a proof.

By the end of this article the reader should be able to do three things the one test demands. First, state what measurably changed: black-white dissimilarity fell from roughly 80 to roughly 55 between 1970 and 2010 while holding in the high 70s in the older industrial metros; the black homeownership rate ended the period near where it began while the white-black gap widened from roughly 25 to roughly 30 points; overt refusal in the testing series fell from common to rare while subtler differentials persisted; disability became the majority basis of complaints at 51.8 percent for 2014; and the adjusted lending disparity settled near 1.6 to 1 with the two largest fair lending settlements in the country’s history at the time following the crisis. Second, name the study series that provides the causal evidence: the Housing Market Practices Survey of 1977 and the Housing Discrimination Studies of 1989, 2000 and 2012, the paired-testing series sponsored by HUD across four decades. Third, confront the corrected fact at the center of the ownership record: the rate is flat and the gap grew, and any version that says otherwise has confused the two. The sections that follow supply the sources, the limits and the counterweights behind each clause of that summary.

What separates the raw denial ratio from the adjusted one?

The raw ratio compares denial rates with no controls, so it mixes discrimination with every legitimate underwriting difference the data omit, especially credit history. The adjusted ratio adds measured controls, 38 loan-file variables in the Boston study, and the remaining gap, about 1.6 to 1, is the disparity the observable economics of the loans do not explain.

Access improved; ownership did not

The five findings converge on the claim this article is built to make, and the claim needs its terms defined before it is stated. Access, in this article’s usage, means the ability to enter a housing transaction without facing refusal or differential treatment on the basis of a protected trait: to be shown the unit, to be quoted the price, to have the application judged on its economics. Ownership means holding the wealth-bearing asset itself, the home whose equity compounds across decades and passes to the next generation. The evidence reviewed here supports substantial reductions in the crudest denials of access: overt refusal fell from common to rare across the testing series, measured black-white separation fell by roughly 25 points on the dissimilarity scale, and the complaint system built by the 1988 amendments processes tens of thousands of cases a year. The same evidence supports no closure of the wealth-bearing gap: the black homeownership rate ended the period where it began, the white-black gap widened by about five points, and the boom-bust of 2004 to 2015 demonstrated how fragile the gains were when they rested on credit terms rather than accumulated equity.

The distinction explains why a statute aimed at transactions could move the first measure and not the second. The Fair Housing Act polices the moment of exchange: the showing, the quote, the application, the loan decision. It does not redistribute the down payment, does not equalize the credit history, and does not transfer the inherited equity that lets one family’s children buy in appreciating neighborhoods while another family’s children start from zero. A black household that faces no discrimination in 2015 still buys with the wealth its parents could accumulate under the conditions of 1970, 1980 and 1990, and those were decades in which the parents’ own access was constrained by the very patterns the testing studies measured. The statute broke the mechanism that reproduced the gap at the point of transaction; it could not reach the stock of wealth the mechanism had already distributed. That is not a defense of the statute’s limits and not an indictment of its design; it is an account of what a transactional civil rights law can and cannot do, stated in the terms the data force.

The counter-readings this article promised to address both fail against this framing, and they fail for opposite reasons. The claim that the statute failed ignores the measured decline in overt exclusion and in the most rigid patterns of separation, ignores the testing series that documented the transformation from refusal to subtlety, and ignores the settlement record that priced the remaining discrimination in the hundreds of millions. The claim that the statute succeeded ignores the ownership gap that widened while access improved, ignores the persistence of extreme segregation in the Ghetto Belt metros, and ignores the erasure of the 2004 peak. Both overreaches select the findings that flatter their conclusion and discard the rest. The record as a whole supports the narrower claim and only the narrower claim: the law changed what happens at the threshold of the transaction, and the threshold was never where the wealth gap lived. A reader who can state that sentence, name the testing series that evidences the first half and the CPS/HVS series that evidences the second, has passed this article’s one test.

The wealth mechanics behind the claim repay a closer look, because they explain why the gap widened while the law operated as written. Homeownership transmits wealth across generations through three channels the statute does not touch. The first is the down payment: a household whose parents own a home can borrow or receive the down payment for its own purchase, while a household whose parents were locked out of ownership must save it from income, a slower path that delays entry and reduces the years of appreciation. The second is credit history: the length and quality of a household’s borrowing record, built over decades, determines the terms on which it can buy, and households whose parents could not borrow on fair terms inherit thinner files. The third is inherited equity itself: the appreciated value of a parent’s home, transferred at death or tapped during life, that finances a child’s purchase outright. Each channel compounds. A white family that bought a suburban home in 1970 watched it appreciate for forty-five years; a black family denied that purchase in 1970, or confined by steering to a neighborhood where appreciation lagged, entered 2015 with less to transfer regardless of how fairly the 2015 transaction was conducted.

This is the flow-versus-stock distinction the article promised. The Fair Housing Act governs flows: the transactions of a given year, the showings, the quotes, the applications. The homeownership gap is a stock: the accumulated outcome of decades of flows, fair and unfair alike. A law that makes each year’s flow fair cannot, by itself, equalize the stocks that decades of unfair flows produced, and it certainly cannot do so within the lifetime of a single enforcement regime. The 2004 to 2015 arc demonstrated the corollary. When credit expanded without equity behind it, the flow looked like progress: the rate rose to 49.1 percent. When the terms of that credit proved predatory and prices fell, the stock reality reasserted itself: the rate returned to 42 percent, and the gap stood five points wider than in 1970. Nothing about that arc suggests the statute was irrelevant; the testing series shows it changed the transaction. Everything about the arc suggests the statute was insufficient to the wealth gap, which was never a transactional problem in the first place.

The Westchester case: a new lever on an old duty

The enforcement record contains one case that changed what the statute’s oldest affirmative duty could do, and it did so through a statute Congress never wrote for housing. United States ex rel. Anti-Discrimination Center of Metropolitan New York v. Westchester County, docket number 06 Civ. 2860 (DLC) in the Southern District of New York, began as a qui tam action under the False Claims Act, 31 U.S.C. section 3729, brought by the Anti-Discrimination Center, a private fair housing organization. The Center alleged that Westchester County, in order to receive more than $50 million in federal housing and community development funds, had falsely certified that it was affirmatively furthering fair housing, the obligation the 1968 act imposes on federal agencies and fund recipients, while ignoring race-based impediments to housing choice and the exclusionary zoning of its municipalities. The false-claims period the Center identified ran from 2000 through 2006. It was the first use of the False Claims Act to enforce a jurisdiction’s affirmatively-furthering obligation, and that novelty is the reason the case belongs in an impact article: it converted a certification the industry had treated as paperwork into a representation with treble-damage consequences.

The procedural history rewarded the gamble. The complaint was filed under seal in April 2006; the Department of Justice initially declined to intervene, and the case was unsealed in January 2007. Judge Denise Cote denied the county’s motion to dismiss on July 13, 2007, holding that an interpretation of the affirmatively-furthering duty that excluded race would be absurd. In early 2009 the court granted partial summary judgment, finding that the county had utterly failed to further fair housing and that its certifications to the federal government were false or fraudulent. The United States intervened after the 2009 opinion. The consent decree the court approved on August 10, 2009 carried a total scope of $62.5 million: the county was required to spend $51.6 million and to develop at least 750 affordable housing units in municipalities with very small black and Latino populations, under the supervision of a federal monitor. The decree did not merely punish the false certification; it directed the remedy at the geographic pattern the certification had concealed, placing affordable units in the whitest jurisdictions rather than concentrating them where affordable housing already existed.

The case’s significance for the impact record is structural rather than numerical. One county’s decree does not move a national dissimilarity index, and this article does not claim that it did. What the case moved was the expected cost of treating the affirmatively-furthering certification as a formality, and it did so by importing the False Claims Act’s machinery, with its private relators and its damages multiplier, into a field that had previously relied on HUD’s administrative process and the Department of Justice’s pattern-or-practice suits. Every jurisdiction that certifies compliance to draw federal funds after 2009 does so against the knowledge that a private organization can test the certification in federal court. The testing studies measure what happens inside the transaction; Westchester measures what happens to the paperwork around it. Together they describe an enforcement regime that, from 1988 forward, attacked discrimination at both levels, and the complaint mix and the settlement record are the aggregate footprints of that regime.

The affirmatively-furthering duty the case enforced is the oldest and vaguest obligation in the statute, which is why the False Claims Act theory was both novel and consequential. The 1968 act requires federal agencies and the jurisdictions that receive their funds to administer programs in a manner that affirmatively furthers fair housing, language that HUD long implemented through a certification regime: each funding cycle, the jurisdiction signs an assurance that it is analyzing impediments to fair housing choice and acting to overcome them. For decades those certifications were treated as paperwork, signed and filed with little federal scrutiny, because the duty’s vagueness made enforcement difficult and HUD’s appetite for confronting its own grantees was limited. The Anti-Discrimination Center’s insight was that the certification, however vague the underlying duty, is a statement of fact submitted to obtain federal money, and the False Claims Act punishes false statements submitted to obtain federal money with treble damages and a private right of action for relators. Judge Cote’s 2007 ruling that excluding race from the duty’s meaning would be absurd supplied the legal bridge: once race was inside the duty, a county that ignored race-based impediments while certifying compliance was making a false claim.

The remedy’s geography is the detail that ties the case back to the segregation record. The decree did not simply extract money; it required the 750 affordable units to be built in the municipalities with the smallest black and Latino populations, the jurisdictions whose exclusionary zoning had produced the pattern the county’s analysis had ignored. That siting choice made the remedy integrative rather than merely compensatory, and the federal monitor gave it teeth beyond the decree’s signing. The United States’ intervention after the 2009 summary judgment ruling signaled that the theory had federal backing, which is what converted a single county’s defeat into a nationwide change in the expected cost of a false certification. Every jurisdiction signing the assurance after August 2009 does so knowing that a private organization can test the statement in federal court and that the damages multiply. The case thus belongs in the impact record not for its effect on any index but for its effect on the price of noncompliance, the channel through which law most reliably changes behavior.

The qui tam mechanism deserves a plain explanation, because it is what made a private organization the enforcer of a public duty. Under the False Claims Act, a private party, called a relator, may file suit on behalf of the United States alleging that someone submitted false claims for federal money; the government may intervene and take over the case or decline, leaving the relator to proceed alone, and a successful action recovers treble damages plus penalties, with the relator receiving a share. The Anti-Discrimination Center filed as relator, the Justice Department initially declined, and the Center litigated the case through the 2007 motion-to-dismiss ruling and the 2009 summary judgment victory before the United States intervened. The structure matters for the impact story: the enforcement innovation was not a new HUD regulation but the discovery that an old anti-fraud statute could be aimed at fair housing certifications, multiplying the damages and deputizing private organizations as prosecutors. The federal monitor appointed under the decree then supplied the ongoing supervision that a one-time damages award could not, reviewing the county’s implementation year by year.

The certification regime the case exposed had operated for decades with minimal scrutiny, and its history explains why the Center’s theory found a receptive court. Since the 1970s, HUD had required jurisdictions receiving community development and housing funds to certify that they were affirmatively furthering fair housing, typically through a written analysis of impediments to fair housing choice updated every few years. In practice, many jurisdictions filed analyses that discussed affordable housing in general terms while saying little or nothing about race, and HUD rarely rejected a certification or tied funds to its quality. The duty’s statutory phrasing, to administer programs in a manner affirmatively to further the purposes of the act, gave HUD latitude it seldom used. Westchester’s analysis, which the court found had utterly failed to consider race-based impediments, was unexceptional in its thinness; what was exceptional was that a relator with the False Claims Act’s damages multiplier chose to test it in court. The case therefore indicted a nationwide practice through a single county’s decree, and the monitor’s ongoing review of Westchester’s compliance became the template for what serious certification would look like.

Did the neighborhood change the child?

The most rigorous evidence on whether neighborhood itself shapes life outcomes comes from an experiment HUD funded in the 1990s, and its findings belong here because the statute’s ultimate justification has always been that where a family lives should not determine what its children become. Moving to Opportunity randomized families living in high-poverty public housing between 1994 and 1998 in five cities, Baltimore, Boston, Chicago, Los Angeles and New York, into three groups: a voucher restricted to census tracts with poverty rates below 10 percent plus counseling assistance, an unrestricted Section 8 voucher, and a control group that continued in public housing. Randomization is what makes the design the strongest causal evidence in the field: because families were assigned by lottery, differences in later outcomes can be attributed to the neighborhood change rather than to the characteristics of families who choose to move.

The interim findings, published while this article’s horizon was still open, were mixed in a pattern the literature has not overturned. The interim evaluation by Orr and colleagues in 2003, and the analysis by Jeffrey Kling, Jeffrey Liebman and Lawrence Katz in Econometrica in 2007, Experimental Analysis of Neighborhood Effects, found no significant effect on adult economic self-sufficiency four to seven years after random assignment: employment and earnings did not move. The same studies found improved mental health among adult female heads of household, no detectable effects on children’s educational outcomes in the Sanbonmatsu and colleagues 2006 analysis, and mixed gendered outcomes for youth, with girls showing improvements on arrests and risky behavior while boys showed worse outcomes on some measures. Jens Ludwig and colleagues, in the New England Journal of Medicine in 2011, found reduced extreme obesity and diabetes among adult women in the experimental group. The long-term follow-up by Ludwig, Greg Duncan, Lisa Gennetian, Katz, Ronald Kessler, Kling and Lisa Sanbonmatsu, in the American Economic Review Papers and Proceedings in 2013, Long-Term Neighborhood Effects on Low-Income Families: Evidence from Moving to Opportunity, reported ten to fifteen years after baseline: improved adult physical and mental health, no detectable effect on economic outcomes or on youth schooling, and substantially improved adult subjective well-being.

The honest summary of the in-horizon record is therefore that moving to lower-poverty neighborhoods improved health and well-being without moving earnings or schooling, a result that complicates any simple story about neighborhoods as destiny while confirming that place affects the body and the mind. Two later developments carry dates the reader should know and a horizon status this article must respect. Raj Chetty, Nathaniel Hendren and Lawrence Katz circulated their analysis of children’s long-run outcomes as National Bureau of Economic Research Working Paper 21156 in May 2015, inside this article’s horizon, finding gains for children who moved young; the journal version appeared in the American Economic Review, volume 106 number 4, pages 855 to 902, in April 2016, two months after this article’s February 1, 2016 reference date, and is named here only as a dated later development, not as an in-horizon finding. The voucher mechanics behind the experiment are surveyed in the companion guide to Section 8 law already linked above.

The design’s details matter because they define what the results can and cannot show. The experimental voucher was restricted to census tracts with poverty rates below 10 percent and came with counseling to help families find and lease units in those neighborhoods; the comparison voucher carried no geographic restriction; the control group stayed in public housing with no voucher. Families volunteered for the lottery, so the results describe the effects of the offer on volunteers, not the effects on all public housing residents, a standard limit of randomized social experiments that the authors state. Take-up was incomplete, many families offered the restricted voucher could not or did not use it, so the published effects are intent-to-treat estimates: the effect of being offered the move, diluted by those who stayed. The effects on families who actually moved, the treatment-on-the-treated estimates the literature also reports, are larger, but the intent-to-treat framing is the conservative one and the one this article’s summary follows.

The gendered pattern in the youth findings is the result that most complicated the early optimism. Girls in the experimental group showed improvements on arrests and risky behavior relative to controls, while boys showed worse outcomes on some measures, a divergence the researchers attributed to differences in how adolescent boys and girls use neighborhood social networks, with boys more exposed to the risks of unfamiliar peer environments. The adult findings were kinder: no gains in employment or earnings, but better mental health for female heads of household, less extreme obesity and diabetes, and, at ten to fifteen years, substantially better subjective well-being. The pattern across all the in-horizon publications is consistent: the neighborhood changed health and happiness without changing the labor market outcomes that determine long-run economic mobility. That boundary is the finding, and the article reports it without the gloss that later commentary sometimes added.

The dated later developments close the section with the horizon discipline this article has maintained throughout. The Chetty, Hendren and Katz working paper of May 2015 sits inside the horizon and may be cited; its journal publication in the American Economic Review in April 2016 sits outside it and is named here only as a later development with its date. The two papers, the 2018 intergenerational-mobility paper in the Quarterly Journal and the 2016 Moving to Opportunity paper in the American Economic Review, must not be conflated. The in-horizon record stands on its own: randomized moves to low-poverty neighborhoods improved the health and well-being of the adults who moved, did not move their earnings or their children’s schooling within the measured window, and left the question of children’s long-run outcomes to research dated after this article’s horizon.

The education null deserves emphasis because it surprised the researchers. The Sanbonmatsu and colleagues analysis in 2006 found no detectable effect of the neighborhood moves on children’s educational outcomes, test scores or schooling attainment, despite the experimental group’s residence in lower-poverty neighborhoods with, on average, better-resourced schools. The result cut against the intuition that motivated much of the policy interest in the experiment: that moving children to better neighborhoods would straightforwardly improve their schooling. Combined with the mixed gendered youth findings and the absence of adult economic effects, the education null defined the boundary of what the in-horizon evidence could claim. Neighborhood changed health, mental health and subjective well-being; it did not change the economic and educational outcomes that determine mobility across generations, at least not within the ten-to-fifteen-year window the follow-up measured. That boundary is stated here without adornment because it is the finding policymakers most needed to hear accurately.

Why does a neighborhood experiment belong in an impact article?

Because the statute’s deepest justification is that place should not fix a child’s prospects, and Moving to Opportunity is the only randomized test of that claim in American housing policy. Its in-horizon findings, health and well-being improved while earnings and schooling did not move, set the boundary of what neighborhood change alone was shown to accomplish.

How to read the sources behind the five findings

A reader who wants to verify this article’s claims rather than take them on trust needs a map of the source landscape, because the five findings come from five different kinds of evidence with five different standards of proof. The segregation finding rests on the decennial census, the most complete enumeration available, analyzed by Glaeser and Vigdor for the Manhattan Institute in January 2012, corroborated by Sander’s block-level work and disciplined by Logan and Stults’s metropolitan tables for the US2010 Project. The census is a count, not an experiment: it shows where people live, not why, and every causal sentence built on it should be read with that limit in mind. The counterweight comes from the Economic Policy Institute’s January 2012 critique, which the article cites not to overturn the trend but to bound its interpretation. A researcher replicating the finding would start with the Census Bureau’s Housing Patterns appendix for the measure definitions and the US2010 Project reports for the metropolitan numbers.

The homeownership finding rests on the Census Bureau’s Current Population Survey and Housing Vacancy Survey, a quarterly survey whose historical table reports tenure by race of householder, anchored at the early end by the 1970 decennial census as reported in Collins and Margo’s 2001 paper. The HVS is a survey with sampling error, not a count, and its quarterly figures move with seasonal and economic noise; the article uses the fourth-quarter 2015 release, published January 2016, as the endpoint because it is the last full measurement inside the horizon. A researcher checking the 41.5 percent figure would pull the HVS historical table for the fourth quarter of 2015 and the Collins and Margo paper for the 1970 census baseline, and would find the same flat line and the same widened gap reported here.

The discrimination finding rests on the four HUD-sponsored testing studies, the only causal series in the set, synthesized for the non-specialist by Oh and Yinger’s 2015 review in Cityscape, HUD’s own research journal. The studies’ reports are public through HUD’s publications office: the 1979 Housing Market Practices Survey volume, the 1991 Housing Discrimination Study synthesis and companions, the 2002 and 2003 HDS2000 volumes, and the June 2013 HDS2012 volume from the Urban Institute. The complaint finding rests on the National Fair Housing Alliance’s annual Fair Housing Trends Report, an advocacy organization’s aggregation of public and private enforcement data, cross-checked here against HUD’s Research Works and the Congressional Research Service’s R44557. The lending finding rests on the most contested ground: a single-metropolitan-area Federal Reserve study from 1992 and 1996, a HUD synthesis, and two Justice Department press releases from 2011 and 2012. The article has reported each source’s limits alongside its numbers, and the ratings in the evidence table, settled, measurable, contested, are the article’s summary judgment on how far each kind of evidence reaches.

The isolation critique also disciplines the failure narrative in a way the article should make explicit. A reader who cites the EPI argument that isolation remained intense has not shown that the statute failed; they have shown that one measure of separation responds more slowly than another when the minority population is growing. The testing series, which measures behavior rather than demography, shows the behavioral change directly, and behavior is what the statute was written to govern. Demography is not. The honest use of the critique is as a bound on interpretation, not as a verdict on the law, and the article has used it exactly that way throughout.

Both overreaches, both wrong

The record this article has assembled punishes two symmetric mistakes, and the article closes its argument by naming them plainly so the reader does not make either. The first overreach says the statute failed. It points to the flat homeownership rate, the widened gap, the Ghetto Belt metros in the high 70s, and the persistence of differential treatment in the 2012 testing round, and it concludes that the law did not work. The evidence against this reading is the testing series itself: a market in which one in three black renters was told nothing was available in 1977 and overt refusal was rare by 2012 is a market the statute changed, and the census decline from 80 to 55 on the dissimilarity scale is not a null result. The enforcement record the 1988 amendments built, tens of thousands of complaints a year, the two largest fair lending settlements in the country’s history at the time, and a False Claims Act case that rewrote the cost of false certification, is not the footprint of a dead letter.

The second overreach says the statute succeeded. It points to the same testing series and the same census decline and concludes that the job is done. The evidence against this reading is the ownership gap that widened from roughly 25 points to roughly 30 points while access improved, the 750-unit Westchester remedy that testifies to how much exclusionary structure survived in one wealthy county alone, and the Moving to Opportunity finding that even randomized moves to low-poverty neighborhoods did not move earnings or schooling within the horizon’s measurements. A law that changed the threshold of the transaction did not change the distribution of the wealth that determines who crosses the threshold on what terms, and the 2004 to 2015 erasure proved that gains built on credit without equity do not survive a crisis.

The article’s position, stated one final time with the sources behind it, is the narrower claim the evidence supports. Access improved and ownership did not. The testing series of 1977, 1989, 2000 and 2012 evidences the first half; the CPS/HVS series and the 1970 census evidence the second. The statute aimed at transactions could not close a gap driven by accumulated wealth, credit and inherited equity, and no honest reading of the five findings extends the law’s reach beyond what it was written to touch. Readers working through the material in a structured way can use a companion study notebook alongside the tables and series named here.

The series thesis thread running beneath this article is the one the brief named: assessing a statute against its own aims and against the aims later observers project onto it. The Fair Housing Act’s own aim, stated in its operative provisions, was to end discrimination in housing transactions. Against that aim the record is favorable: the testing series documents the transformation of the transaction from refusal to subtlety, the census documents the decline in the most rigid separation, and the enforcement system built in 1988 processes the violations its design makes visible. The projected aim, that the statute would close the racial wealth gap as expressed in homeownership, was never in the operative provisions, and the record is correspondingly unfavorable: the rate flat, the gap wider, the gains of the boom erased. Confusing the two aims produces both overreaches at once, the failure narrative that ignores the transaction and the success narrative that ignores the wealth. The article’s discipline has been to keep each finding attached to the aim it actually tests.

A final word on what this article does not do. No finding reported here is extended to any current policy, and none is presented as a recommendation. The figures are dated, sourced and measured; the trends end at the horizon; the later developments are named with their dates and fenced off from the findings. The reader who wants to argue about what should be done next will find in these pages the evidence the argument must reckon with and nothing more: five findings, four studies, two settlements, one experiment, and the distinction between the rate that did not move and the gap that grew. That is what measurably changed, and what did not, in the decades after 1968.

Frequently Asked Questions

Q: Did the Fair Housing Act reduce segregation?

The census evidence shows that black-white residential segregation declined substantially after the act’s passage, though the decline cannot be credited to the statute alone. The national black-white dissimilarity index fell from about 80 in 1970 to about 55 in 2010, according to Edward Glaeser and Jacob Vigdor’s January 2012 Manhattan Institute report covering thirteen censuses from 1890 through 2010, and it fell in all eighty-five of the largest cities. Richard Sander’s independent analysis found average block-level dissimilarity across sixty major metros falling from 0.92 in 1970 to 0.70 in 2010. The decline coincided with the act’s enforcement, with the 1988 amendments, and with broader demographic and economic shifts, so the statute’s precise contribution cannot be isolated. Older industrial metros including New York, Chicago, Detroit, Newark, Milwaukee, Gary, Cleveland, and St. Louis remained in the high seventies in 2010, which counts as extreme.

Q: Did the Fair Housing Act close the homeownership gap?

No. The black homeownership rate sat in the 41.6 to 42.1 percent range in 1970 on the decennial census and in the 41.5 to 41.9 percent range in 2015 on the Census Bureau’s Current Population Survey and Housing Vacancy Survey, essentially unchanged across five decades. Because the white rate rose over the same span, from 66.8 percent to 72.1 percent for non-Hispanic whites, the white-black gap widened from about twenty-five percentage points to about thirty. The black rate did peak at 49.1 percent in 2004 during the housing boom before the foreclosure crisis erased the gains. The precise framing matters: the rate stood still while the gap grew. A transaction statute can open access to purchases, but homeownership at the national level depends on income, credit, and inherited equity that anti-discrimination rules do not supply.

Q: What do paired testing studies show about fair housing?

The four federal studies, the Housing Market Practices Survey of 1977, the Housing Discrimination Study of 1989, the Housing Discrimination Study of 2000, and the Housing Discrimination Study of 2012, show a consistent directional pattern across four decades. Overt refusal declined sharply: in 1977 about one in three black renters and one in five black homebuyers were told nothing was available, while by 2012 outright refusal was rare. Subtler differential treatment persisted: in the 2012 study, black renters were told about 11.4 percent fewer units and shown 4.2 percent fewer, and black homebuyers were shown about 18 percent fewer homes than white testers. The studies also establish why complaint counts understate incidence: a homeseeker shown fewer units cannot know what a white tester was shown. Methodological differences across the four studies prevent precise trend comparisons, so only qualitative trends can be drawn.

Q: How many fair housing complaints are filed each year?

The National Fair Housing Alliance’s Fair Housing Trends Report, 2015 edition, published in April 2015 and covering calendar year 2014, counted 27,528 complaints nationwide across all intake systems, with 14,272 alleging disability discrimination and 6,044 alleging race discrimination. The Alliance aggregates complaints processed by private fair housing organizations, state and local Fair Housing Assistance Program agencies, the Department of Housing and Urban Development, and the Department of Justice, and private organizations process the large majority. HUD cautions that a single case may allege multiple bases, so percentages by basis can sum past one hundred percent. Annual totals move with enforcement capacity and with the visibility of violations rather than with the underlying incidence of discrimination, which the paired testing studies measure separately. The complaint record describes the enforcement system’s intake, not the market’s behavior.

Q: Which protected class files the most fair housing complaints?

Disability. The National Fair Housing Alliance’s 2015 Trends Report, covering 2014, found disability-based discrimination alleged in 51.8 percent of all complaints nationwide, with race second at 22.0 percent. Within HUD’s own intake the disability share was 53.2 percent. The Congressional Research Service’s report R44557 notes that disability has been the largest single basis since fiscal year 2005, and HUD’s Research Works publication reported a disability plurality for 2005 through 2008 as well. The ordering follows from the 1988 amendments, which added disability and familial status as protected classes and created duties whose violation the affected person can see, such as the duty to permit reasonable accommodation. A tenant denied an assistance animal knows it happened. A homebuyer shown fewer listings does not. The mix therefore reflects the visibility of violations, not a ranking of how much discrimination each group faces.

Q: Did fair housing enforcement change lending discrimination?

The evidence shows enforcement narrowed but did not eliminate measured lending disparities, and the largest settlements came decades after the statute’s passage. The Federal Reserve Bank of Boston’s study by Munnell and colleagues found that the raw 1990 HMDA denial ratio of about 2.7 to 1 in the Boston metro fell to about 1.6 to 1 after controlling for thirty-eight additional underwriting variables, leaving black and Hispanic applicants about sixty percent more likely to be denied. The Department of Justice’s post-crisis settlements, $335 million with Countrywide announced December 21, 2011, and $175 million with Wells Fargo announced July 12, 2012, addressed steering and pricing discrimination in 2004 through 2009 lending. Those cases show the enforcement apparatus reaching large-scale lending discrimination, while the persistence of an adjusted gap shows that enforcement and disclosure together did not erase the disparity.

Q: What is the Westchester fair housing case about?

United States ex rel. Anti-Discrimination Center of Metropolitan New York v. Westchester County, filed in the Southern District of New York, was a qui tam action under the False Claims Act alleging that Westchester County falsely certified compliance with its duty to affirmatively further fair housing while obtaining more than fifty million dollars in federal housing and community development funds during 2000 through 2006. The Anti-Discrimination Center alleged the county ignored race-based impediments and exclusionary municipal zoning. Judge Denise Cote denied dismissal in July 2007, granted partial summary judgment in early 2009 holding the county had utterly failed its obligations and its certifications were false or fraudulent, and the consent decree approved August 10, 2009 required $62.5 million in total scope, $51.6 million in county spending, at least 750 affordable units in low-minority municipalities, and a federal monitor. It was the first use of the False Claims Act to enforce the affirmatively furthering duty.

Q: Does neighborhood matter for children’s outcomes in fair housing research?

The Moving to Opportunity experiment, which randomized public housing families in five cities between 1994 and 1998 into voucher and control groups, provides the causal evidence. Interim analyses found no detectable effects on youth schooling and mixed gendered results on behavior. The long-run analysis released as National Bureau of Economic Research Working Paper 21156 in May 2015, published in the American Economic Review in April 2016, found that children who moved to lower-poverty neighborhoods at young ages earned more as adults, with the gains fading for children who moved as teenagers. Because the April 2016 journal version postdates this article’s February 2016 reference date, the article treats it as a later development and relies on the in-horizon interim findings, which showed improved adult health and well-being but no detectable economic effects at ten to fifteen years. Randomization is what makes the evidence causal rather than correlational.

Q: How is the dissimilarity index measured?

The dissimilarity index is computed from census tract or block data within a metropolitan area. For two groups, it sums the absolute differences between each neighborhood’s share of the metro’s group members and its share of the comparison group, then halves the total, producing a value from zero to one hundred. Conceptually it is the percentage of one group’s residents who would have to move between neighborhoods for every neighborhood to match the metro’s overall composition. The U.S. Census Bureau’s Housing Patterns appendix confirms the zero to one hundred range and the interpretation. By the convention Douglas Massey and Nancy Denton set out in 1993, values from zero to thirty count as low segregation, thirty-one to sixty as moderate, and sixty-one to one hundred as high. On the zero to one reporting scale the same thresholds appear as decimals.

Q: Why did Hispanic and Asian segregation trends diverge after 2000?

Between 1980 and 2000, both Hispanic and Asian segregation tended to rise, with larger increases for Asians, according to the 2002 Census Bureau working paper by Iceland, Weinberg, and Steinmetz. Between 2000 and 2010, the paths split: Logan and Stults found Asian-white dissimilarity rising from 42.1 to 45.9 while Hispanic-white dissimilarity sat roughly flat, moving from 51.6 to 50.0. Part of the explanation is compositional. Both populations grew substantially through immigration, and new arrivals concentrate in gateway neighborhoods, which raises measured separation even without any change in discriminatory behavior. The Hispanic flattening may also reflect longer settlement histories and broader geographic dispersion in the 2000s. The divergence is a reminder that the index measures residential patterns, not motives, and that identical index movements can arise from different causes.

Q: How did the 1988 amendments change fair housing enforcement?

The Fair Housing Amendments Act of 1988, Public Law 100-430, signed September 13, 1988, rebuilt an enforcement scheme the original 1968 act had left weak. It added disability, termed handicap in the statute, and familial status as protected classes, joining race, color, national origin, religion and sex, the last added in 1974. It gave the Department of Housing and Urban Development authority to process administrative complaints heard by administrative law judges, with civil penalties and injunctive authority, replacing a conciliation-only regime that could investigate but not compel. It strengthened the Department of Justice’s pattern-or-practice litigation power. Analysts date serious enforcement to 1988 rather than 1968 for this reason, and the complaint record bears the amendment’s signature: disability, a class the amendments created, accounted for 51.8 percent of complaints reported for calendar 2014, the direct enforcement footprint of the expanded statute.

Q: How large were the Countrywide and Wells Fargo fair lending settlements?

The Countrywide settlement, announced December 21, 2011, totaled $335 million and was described by the Department of Justice as the largest residential fair lending settlement in history at the time. It covered 2004 through 2008 lending and alleged that more than 200,000 black and Hispanic borrowers were charged higher rates and fees or steered into subprime loans despite qualifying for prime credit, with the case filed in the Central District of California. The Wells Fargo settlement, announced July 12, 2012, totaled $175 million and was described as the second largest fair lending settlement at the time. It covered 2004 through 2009 loans to about 34,000 black and Hispanic borrowers in thirty-six states and the District of Columbia, directing $125 million to borrower compensation and $50 million to down payment assistance, without an admission of wrongdoing. Both arose from crisis-era lending.

Q: What was the Moving to Opportunity experiment?

Moving to Opportunity was a HUD-funded demonstration that used random assignment to test whether moving to lower-poverty neighborhoods improves family outcomes. Between 1994 and 1998, families living in high-poverty public housing in Baltimore, Boston, Chicago, Los Angeles, and New York were randomized into three groups: a voucher restricted to census tracts with poverty below ten percent plus housing counseling, an unrestricted Section 8 voucher, or a control group remaining in public housing. Because assignment was by lottery, later differences between groups can be attributed to the move rather than to self-selection. Interim results at four to seven years showed no significant effect on adult economic self-sufficiency but improved adult mental health. At ten to fifteen years, researchers found improved adult physical and mental health and well-being with no detectable economic effects.

Q: Why did the black homeownership rate fall after 2004?

The black homeownership rate peaked at 49.1 percent in 2004, measured in the Census Bureau’s Housing Vacancy Survey series, then fell through the foreclosure crisis until every point of the gain was erased and the rate returned to about 42 percent by 2015. The boom-bust arc reflects how the gains were financed: the Department of Justice’s post-crisis settlements documented that Countrywide steered more than 200,000 black and Hispanic borrowers into subprime products or higher rates and fees than their qualifications warranted in 2004 to 2008 lending, and Wells Fargo’s 2012 settlement covered similar patterns for about 34,000 borrowers from 2004 to 2009. Ownership built on disadvantageous credit terms proved fragile when prices fell. The erasure is central to the article’s claim: access to the transaction improved while the wealth-bearing asset did not accumulate, because the statute polices the exchange and cannot supply the equity that sustains ownership through a downturn.

Q: What do disability fair housing complaints usually involve?

Disability complaints most often involve a housing provider’s failure to meet the affirmative duties the 1988 amendments created: refusing a reasonable accommodation, such as an assistance animal in a no-pets building or a reserved accessible parking space, refusing a reasonable modification of the unit at the tenant’s expense, or applying rules that screen out people with disabilities. Design and construction violations in newer multifamily buildings also generate complaints. These violations are visible to the person affected, which is why they dominate the complaint record: the National Fair Housing Alliance’s 2015 Trends Report attributed 51.8 percent of 2014 complaints to disability. The visibility mechanism cuts both ways. It means the complaint system captures disability discrimination relatively well, and it means the system’s low race share cannot be read as evidence that race discrimination is rare, since steering and differential treatment are invisible without paired testing.

Q: What did the Boston Fed study find about adjusted lending disparities?

The Federal Reserve Bank of Boston study by Alicia Munnell, Geoffrey Tootell, Lynn Browne, and James McEneaney, published as a working paper in 1992 and in the American Economic Review in 1996, started from 1990 Home Mortgage Disclosure Act data for the Boston metropolitan area showing minority applicants denied at about 2.7 times the white rate. The researchers then collected thirty-eight additional variables from the underlying loan files, including credit history, loan-to-value ratios, and employment characteristics, and re-estimated the model. The disparity fell to about 1.6 to 1, meaning black and Hispanic applicants remained about sixty percent more likely to be denied than white applicants with comparable measured characteristics. A HUD USER literature review reported a related estimate of about eighty percent higher denial probability with loan, property, and applicant controls. The study covers one metro, and its specification was contested.

Q: What are the limits of HMDA data for measuring discrimination?

The Home Mortgage Disclosure Act data that made lending disparities visible omit the variables lenders say determine creditworthiness, above all credit history, along with other underwriting factors. That omission is the industry’s standard criticism of every raw HMDA disparity: a denial gap can reflect legitimate differences in applicant risk profiles that the dataset does not record, so the raw ratio, about 2.7 to 1 in the Boston Fed study’s 1990 data, cannot by itself prove discrimination. The Boston researchers answered the criticism by collecting 38 additional variables from loan files and re-estimating, which cut the disparity to about 1.6 to 1, but the adjusted figure still rests on measured controls and cannot capture unmeasured ones. The study was also confined to the Boston metropolitan area with contested methods. The responsible use of HMDA, which this article follows, reports the raw and adjusted figures together, states what the data omit, and treats neither as proof in any individual case.

Q: Did Moving to Opportunity improve adults’ economic outcomes?

No, on the in-horizon evidence. The interim analysis by Kling, Liebman, and Katz in 2007 found no significant effect on adult economic self-sufficiency four to seven years after randomization. The long-term analysis by Ludwig and colleagues in the 2013 American Economic Review Papers and Proceedings found no detectable effect on economic outcomes or youth schooling ten to fifteen years after baseline, even as the same study found substantially improved adult physical and mental health and subjective well-being. A 2011 New England Journal of Medicine paper by Ludwig and colleagues found reduced extreme obesity and diabetes among adult women. The pattern is consistent across the in-horizon studies: moving to lower-poverty neighborhoods improved health and well-being without improving earnings or employment. A May 2015 working paper on children’s long-run earnings is named in the article as a later development.

Q: How does the isolation index differ from the dissimilarity index?

The dissimilarity index measures evenness: how unevenly two groups are distributed across neighborhoods, expressed as the share of a group’s residents who would have to move for every neighborhood to mirror the metro’s composition. The isolation index measures exposure: the probability that a randomly chosen member of a group shares a neighborhood with another member of the same group. A metro can score better on evenness while group members still live in neighborhoods dominated by their own group, which is why the Economic Policy Institute’s January 2012 critique of the Glaeser and Vigdor findings emphasized that isolation remains intense in many places where dissimilarity has fallen. Both indices come from census geography and both appear in the federal segregation literature, but they answer different questions, and the article’s segregation finding rests on dissimilarity while noting the isolation counterweight.

Q: What did the 1977 Housing Market Practices Survey find?

The first federal paired-testing study set the baseline against which the entire series is read. The Housing Market Practices Survey, fieldwork in 1977 and published by HUD in 1979 as Measuring Racial Discrimination in Housing Markets, ran roughly 3,264 tests in 40 metropolitan statistical areas with black and white testers only. As summarized by Oh and Yinger in 2015, it found overt refusal on a scale that later rounds would never again record: one in three black renters and one in five black homebuyers were told that nothing was available. The study measured the market nine years after the Fair Housing Act’s passage and before the 1988 amendments rebuilt enforcement, when HUD could investigate and conciliate but not compel. Every later round, the 1989, 2000 and 2012 Housing Discrimination Studies, is interpretable only against this starting point, and the transformation the series documents, from refusal at the threshold to subtle differences in units mentioned and shown, begins with the bluntness the 1977 survey captured.