The Policy Experiment: What the Right to Request Changed
This chapter examines the United Kingdom’s 2014 expansion of the Right to Request Flexible Work and asks what kind of change a statutory right can actually produce. The useful distinction is between being eligible to ask, having flexible arrangements available at work, using one, and changing a care arrangement as a result. Keeping those stages separate lets the reader interpret the study’s evidence without treating a legal entitlement as an automatic schedule—or mistaking a worker’s pre-existing characteristics for a policy effect.
A right to request, not a right to receive
Flexible work was not created in the UK in 2014. The statutory right first applied to parents of young or disabled children. Later changes extended it to some employees caring for dependent adults and broadened the age range for children. Those steps still left many workers outside the system, particularly people dealing with adult-care needs who did not fit a narrow eligibility category.
The Children and Families Act 2014 changed the reach of the Right to Request Flexible Work. From 30 June that year, an employee with at least 26 weeks of continuous service could formally request a change to their working arrangements. The policy no longer targeted only a selected family circumstance; it became a right available to all eligible employees, including people supporting an adult with a disability or long-term health condition. The IZA study estimates that this change expanded eligibility to more than 20 million workers.
The arrangements covered a range of ways of reorganising work: job sharing, working from home, compressed hours, flexitime, and part-time work. That list matters because “flexibility” is not one treatment with one predictable effect. A later start can help with a morning appointment. Working from home can reduce the cost of being present between care tasks. Compressed hours can create a day away from work, but may make the remaining days more demanding. Part-time work can create time while also reducing income and possibly changing career prospects. The policy opens a route to negotiation; it does not determine which route a worker takes.
Nor does the right guarantee that the route will be open. The 2014 rules simplified the procedure and required employers to handle requests reasonably, but employers could still refuse on recognised business grounds. An employee in an occupation that depends on fixed staffing, physical presence, or tightly sequenced shifts may have less room to change when or where work happens than an employee whose tasks can move across time or location. A manager’s response and the culture around disclosure also influence whether a worker sees the right as usable.
This creates four stages that should not be collapsed into one:
- Eligibility: the worker falls within the statutory right to make a request.
- Availability: the workplace offers one or more forms of flexible working, whether through the formal right or existing practice.
- Use: the worker actually takes up an arrangement.
- Care consequence: the change in work timing, location, or control alters who provides care, how much they provide, or how the household shares it.
The study is interested in the fourth stage, but it needs to establish the second and third first. If the reform changed neither workplace availability nor employee use, a later care result could not plausibly be attributed to increased flexibility. Conversely, an increase in use would not by itself show that anyone’s care arrangements changed. It would only show that the policy reached working conditions, creating the possibility of a downstream effect.
This distinction also clarifies what the study’s comparison does and does not mean. The employees without pre-reform access are not a group that lacks initiative, and the employees with access are not a naturally more adaptable control population. They occupy different workplace environments, and those environments may reflect occupation, industry, employer size, management practice, or prior expectations about who should be available outside work. The evaluation tries to compare changes between groups after accounting for measured differences; it does not turn flexibility into a personal virtue or inflexibility into a personal failing.
It also means that a policy effect can be present even if the legal language is only one part of the change. A new right may give an employee a reason to raise a request, give a manager a clearer framework for responding, or make informal accommodations seem more legitimate. The study measures some of this through reported availability and use, including informal flexible arrangements. It cannot determine which of these channels mattered for each person, but it can test whether exposure to the reform coincided with a measurable change in working conditions before asking about care.
The 2014 rule is also distinct from later law. The IZA paper notes that an amendment taking effect in April 2024 made flexible working a “day one” right. That later change should not be projected backward into the study: the evidence here concerns the 2014 expansion and its 26-week eligibility condition. This distinction is more than legal housekeeping. Changing who can ask, and when they can ask, changes which workers are exposed to the policy and therefore changes the question an evaluation answers.
How a legal change becomes evidence
To estimate what the reform changed, the study uses the UK Household Longitudinal Study, a panel survey that follows people over time and records employment, health, family circumstances, and caregiving. The analysis uses Waves 1 through 9, covering the years before and after the 2014 expansion. Later waves are excluded to avoid bringing the very different conditions of the COVID-19 period into the comparison.
The main sample contains 5,048 people observed in paid employment throughout the study period. That choice makes the care question sharper: the researchers can look at changes in care while holding employment attachment in view, rather than mixing a change in care with a person entering or leaving a job. It also creates a boundary. The study does not estimate whether the reform prevented workers from leaving employment, helped people return after a care break, or changed the choices of people who were not continuously employed.
The comparison is based on workplace access before the reform. Employees who reported that no flexible working arrangement was available to them are classified as newly exposed when the universal right arrives. Employees who already had at least one arrangement available form the comparison group. The point is not that the second group is “untreated” in every sense; they already had some flexibility. It is that the 2014 reform relaxed a binding constraint more sharply for the first group than for the second.
That definition produces a policy-exposure estimate rather than a simple comparison of people who use flexibility with people who do not. Some employees newly exposed to the right may never request an arrangement. Others may request one and be refused. Still others may use an arrangement for reasons unrelated to care. The estimated effect therefore captures the average consequence of being in a workplace whose access to flexibility was expanded by the reform, not the effect of a single named arrangement for a worker who certainly received it. This is the right level of interpretation for a statutory policy: it includes the institutional response as well as individual take-up.
Those groups were not identical to begin with. Before matching, the previously inflexible group contained more men and more workers in semi-routine occupations and industries such as manufacturing, construction, and accommodation and food services. Age and education also differed. These differences matter because the same characteristics can affect both access to flexible work and the likelihood of providing care. If they were ignored, a later difference might reflect occupation or household composition rather than the reform.
The researchers therefore first use propensity-score matching. In plain language, they match workers with different pre-reform access profiles while taking account of characteristics such as age, gender, marital status, education, occupational classification, industry, and other baseline conditions. The regression models also include these covariates, along with individual and time fixed effects. Matching cannot make the groups identical in every respect, but it reduces measured imbalance before the main comparison.
The main estimate comes from a difference-in-differences design. This compares the change over time for workers newly exposed to the reform with the change over time for workers who already had access. The underlying question is: after the policy date, did the first group move differently from the second group? The method is credible only if, without the reform, the two groups would have followed broadly parallel paths. An event study examines that assumption by plotting effects at different distances from the policy date. In the study, the pre-reform coefficients are generally close to zero and statistically insignificant, which supports—but does not prove—the parallel-trends assumption.
A second sample focuses on potential caregivers. These are 1,205 employed people who, before the reform, reported at least one family member with a disability or long-term health condition requiring care. The category is deliberately about a care connection, not a promise that the respondent will become the main carer. A person may share care, arrange paid support, provide help outside the household, or decide that someone else can meet the need. This subgroup lets the study ask whether flexible work has a different effect when a worker already has a plausible care demand nearby.
The logic can be represented as a chain, with the point of uncertainty made explicit:
The first-stage results show that the chain begins with a measurable change in working conditions. In the total sample, the number of flexible arrangements available increased by about 0.53 for men and 0.87 for women. The probability of using any flexible arrangement rose by 13.3 percentage points for men and 21.2 points for women. Use of informal flexibility—arrangements that may not be part of a formal statutory request—also rose, by 6.5 points for men and 9.4 points for women. The reform appears to have changed workplace practice, not only the wording of the law.
The potential-caregiver group shows a similar first stage. The number of available arrangements increased by 0.649 for men and 0.812 for women. Use of any arrangement rose by 10.0 percentage points for men and 21.6 points for women. Among potential caregivers, use of informal flexibility increased by 11.4 points for men and 7.9 points for women, although the reported statistical strength differs across those estimates.
These numbers are best read as evidence that the policy reached the workplace, not as evidence that workers received equal relief. They come from self-reported access and use, and the measures combine several forms of flexibility. They do not identify which arrangement each worker received, how long it lasted, whether it was approved formally, or whether it matched the care need. A worker may gain control over start times but still be unable to cover an overnight need; another may work from home but remain unable to leave a meeting for an emergency. The first stage establishes increased exposure to flexibility, not equal relief from every work–care conflict.
The design has further limits. It is not a randomized experiment, because access to flexible work was shaped by workplaces and workers before the reform. Matching and fixed effects address measured differences and stable individual differences, while the event study provides a check on pre-reform trends. They cannot rule out every time-varying difference, such as an industry shock or a change in management that happened alongside the policy. Care and flexibility are also reported by survey respondents, so recall and reporting differences may affect the estimated magnitude.
Even with those qualifications, the design improves the question. Instead of asking whether people who work flexibly are generally more likely to care, it asks whether a policy that expanded access changed outcomes for workers who previously lacked it, relative to workers who already had some access. That is a narrower claim, but it is more useful for judging the reform. It also prepares the evidence for a more discriminating test: whether the people affected provide care within or outside the household, whether they cross an intensive-care threshold, and whether men and women adjust in the same way.
The first-stage result therefore does not settle who provides adult care. It establishes that the policy changed a relevant input into that decision. The next result must be read at the level of care margins, where a small average effect may conceal a meaningful change in which family member participates or in how much of the most demanding work one person carries.