The UK Test: What Changed When Firms Had to Publish
The UK gender-pay-gap reporting rule provides the clearest causal test in this material of what public pay transparency can do. This chapter reconstructs the rule and the study built around its 250-employee threshold, so the reader can separate the policy’s institutional treatment from the measured result and judge exactly how far that result travels.
The question is not simply whether the reported gap went down. It is whether firms that were required to publish changed the pay outcomes of their workers relative to similar firms that were not required to publish, and whether the research design can distinguish that change from ordinary differences between larger and smaller employers.
A threshold turned pay into public information
The policy emerged from a UK consultation on pay transparency that began in 2015. In February 2017, the government adopted regulations requiring firms registered in Great Britain with at least 250 employees to publish gender-equality indicators. The rule applied to both private and public employers in England, Wales and Scotland; it did not apply in Northern Ireland. Organisations belonging to a group had to report individually rather than allowing a parent company’s result to stand in for every subsidiary.
The threshold was defined using the firm’s employee count on April 5, the end of the UK financial year. A firm that reached at least 250 employees on that date had to calculate the indicators and publish them by April 5 of the following year. The employee definition was deliberately extended to include agency workers. Part-time workers counted with the same weight as full-time workers in the indicators, while partners were included in the headcount but excluded from the calculation itself.
The required indicators were designed to make the shape of the pay distribution visible. Firms had to report the gender gap in mean and median hourly pay, expressed relative to men’s pay; the mean and median bonus gap; the proportion of men and women receiving any bonus; and the proportion of women in each quartile of the pay distribution. A reader could therefore see more than an overall wage average. The quartile measure indicated where women sat in the firm’s pay hierarchy, while the bonus measures showed whether access to variable pay differed by gender.
That information still had limits. The firm-level measures were not adjusted for occupation, tenure, hours or responsibility, and they did not identify which decisions generated the gap. A company with few women in senior roles could report a large difference even if people doing comparable work were paid similarly. A company with compressed pay at lower levels could report a smaller overall gap while still offering women less access to promotion or high-value work. Publication created a signal for scrutiny, not a complete diagnosis.
What made the UK rule distinctive was where the signal went. Firms had to publish on their own websites and on a dedicated government website. The information could therefore be encountered by employees, jobseekers, journalists, customers, investors and other firms, not only by an internal HR team or a works council. The policy covered roughly 10,500 firms—about 0.4% of all UK firms—but those firms represented around 40% of employment and 48% of turnover. A narrow slice of the business population could thus produce a broad public conversation about employer performance.
The timing reinforced the effect. Media outlets reported the first results, sometimes identifying employers with especially large gaps. Google searches for “gender pay gap” spiked around the first reporting deadline, and public attention rose again around later deadlines. The researchers describe this as an information shock: many employers had not previously calculated the gap, and very few firms below the threshold voluntarily published comparable figures. The policy changed not only what firms knew about themselves, but also what outsiders could compare.
The publication obligation was not the same as a duty to improve the number. The Equality and Human Rights Commission could seek court orders and unlimited fines from firms that failed to publish, but the regulations did not impose a sanction simply because a firm’s gap remained large or failed to improve. This distinction is essential. The UK rule created a credible requirement to disclose, while leaving much of the pressure to workers, public audiences, market participants and the firm’s own judgment.
There was also an interruption. In March 2020, during the coronavirus outbreak, the government temporarily lifted the requirement. Just over half of the firms expected to publish that year had done so before the pause, and firms began publishing again in October 2021. The interruption gave the researchers an additional piece of context: when publication stopped and public attention shifted to the pandemic, the estimated policy effect became somewhat smaller in the available payroll data. That pattern is consistent with a disciplinary role for visibility, although it is not by itself a separate causal proof of the mechanism.
The sequence distinguishes three events that are easy to collapse: the government’s rule, the firm’s publication, and the researchers’ estimate. Public attention may be part of the policy’s practical effect, but the payroll comparison is what identifies the measured wage change. The design does not observe every conversation or decision that follows a report.
Why compare firms just above and below the cutoff?
A simple before-and-after comparison would be weak. Pay gaps might have changed because of the wider economy, a shift in the composition of industries, the pandemic, or a general trend affecting large employers. A comparison between all reporting and non-reporting firms would also be problematic because firms above 250 employees differ from smaller firms in many ways: they may have more formal HR systems, different occupations, more public visibility and different wage-setting structures.
The study narrows the comparison. It uses the Annual Survey of Hours and Earnings, an employer survey covering about 1% of the UK workforce, and follows workers’ pay and employment information over time. The main estimation window runs from 2013 through 2021. The researchers compare workers in firms with between 200 and 300 employees, placing firms just below the legal threshold in the control group and firms at or above it in the treated group.
The intuition is local rather than universal. An employer with 249 employees and an employer with 251 employees may still differ, but they are more plausibly comparable than a 20-person firm and a multinational with thousands of workers. If the two groups were moving in parallel before the rule, and only one group became subject to the publication requirement, a later divergence in the gender pay gap is evidence consistent with the policy causing that divergence.
The researchers define treatment status using firm size in 2015, before the implementation process began. This choice reduces the risk that a firm’s later response to the rule changes its own treatment status. It also recognises that firm size can be endogenous: an employer might grow past the threshold, shrink below it, or adjust its headcount in anticipation of reporting. The pre-policy definition therefore provides a more stable basis for comparison than a classification based on a firm’s later, potentially affected size.
The regression also compares women and men within those firms. Individual-by-firm fixed effects absorb characteristics of a particular worker-employer match that do not change over time. The key coefficient asks whether the gender difference in outcomes changed more in treated firms than in control firms after the reporting rule began. That is why the design is often described as a triple difference: it uses differences across firms, over time, and by gender.
This method does not require the authors to claim that the threshold itself is magical. It requires a credible counterfactual: absent the reporting obligation, workers in firms just above the cutoff would have experienced a similar evolution in the gender gap to workers in firms just below it. The study checks that premise in several ways.
First, the event studies show comparable pre-policy evolution in the gender pay gap and in men’s and women’s pay separately. There is no clear evidence that treated employers began changing pay before the first reporting deadline. Second, placebo regressions apply the same method to artificial firm-size thresholds. None of those placebo mandates produces a significant gap effect, which makes it less likely that the result is simply a general shock affecting larger firms differently. Third, changing the bandwidth around the threshold leaves the estimated gap effect broadly similar until the comparison becomes too wide. The results also remain broadly stable when the researchers vary the year used to define firm size, add age controls, change regional to industry-specific time effects, restrict the sample to full-time or private-sector workers, use labour-force weights, or include 2017 in the treatment period.
These checks strengthen the interpretation, but they do not remove every limitation. The Annual Survey of Hours and Earnings observes only sampled workers rather than every employee in a firm. The study therefore cannot use that source to construct a complete firm-level pay gap in the same way the public reporting data do. The main estimate is local to firms near the 250-employee threshold, not an average effect for every UK employer. The policy also reached public audiences unevenly, and the pandemic reduced the number of observations in later years. A stronger result would need evidence from more firms, longer follow-up and more direct measures of how employees and employers used the published information.
What the measured result represents
Within those boundaries, the central estimate is clear. The policy produced a statistically significant relative increase of about 3 percentage points in women’s hourly pay compared with men’s pay in treated firms. Relative to the pre-policy gender gap in the study’s estimation sample, that corresponds to a 19% reduction. The result is not a claim that every UK firm reduced its gap by 19%, nor that the economy-wide gender pay gap fell by that amount.
The separate gender estimates explain the direction. Men’s real pay in treated firms grew about 2.9% more slowly than men’s pay in the control firms after the policy. The average effect on women’s pay was not statistically significant. The most defensible summary is therefore that public reporting narrowed the measured gap near the threshold, primarily through a slowdown in men’s pay growth rather than a broad increase in women’s pay.
That distinction changes the policy question. If the objective is to reduce a statistical gap, the rule appears to have worked in this setting. If the objective is to raise women’s earnings, improve women’s access to high-paying work, or correct unequal evaluation, the result is incomplete. A firm can make its reported gap smaller by changing the growth path of higher-paid men while leaving the pay and opportunities of women largely unchanged. The number moves, but the distributional meaning of the movement must still be judged.
The UK test consequently establishes something narrower and more useful than a slogan. A salient public reporting obligation can change employer pay dynamics under conditions where firms near a size threshold are compared over time. The evidence does not show that publication alone explains every response, that the result applies to all transparency designs, or that a smaller gap automatically means a fairer workplace. It gives us a credible starting point for the next question: which pay decisions moved inside the firm, and what did the adjustment mean for workers?