Sweden’s Motivational Email Experiment: Support, Pressure, and Context
The Swedish case is a test of whether a public employment service can sustain job search by changing the way it speaks to unemployed people. This chapter follows the intervention through the relationship in which it operated: a system that required monthly activity reports and monitored compliance, but also wanted people to make the applications and decisions that lead to work. That sequence makes the result legible. The emails were noticed, and reporting increased, yet the downstream search response did not improve in the way the intervention intended.
The institutional setting made reporting consequential
In Sweden, people receiving unemployment insurance were expected to register with the Public Employment Service, remain available for work, search actively, and document their efforts. The documentation was not an optional survey for researchers. Each month, a job seeker submitted a digital activity report through an electronic identity system. The report included activities such as applications for posted vacancies, spontaneous applications, and interviews, and it was electronically signed before submission.
The report connected the job seeker to the enforcement side of the system. Public Employment Service caseworkers reviewed the submissions and could notify the relevant unemployment-insurance fund when activity appeared insufficient. The fund made the final decision about a benefit sanction. Missing meetings, failing to submit a report, rejecting a suitable job, or violating other requirements could therefore have consequences for income support. The service had also added risk-based algorithms, specialized staff focused on detecting violations, and profile-specific ranges for the number of applications expected each month.
This background matters because it gives the first-stage outcome a particular meaning. A report submission may reflect genuine search, but it may also reflect a person responding to a formal obligation. The environment was already relatively controlling before the study emails arrived. The authors note that Sweden ranked fifth strictest among 38 countries in a 2022 comparison of reporting and monitoring procedures. A message about job search was therefore never just a message about job search; it came from an institution that could observe the recipient’s activity and affect benefit eligibility.
The field experiment was built around that existing system. It covered 200,720 newly unemployed job seekers who entered the Swedish Public Employment Service between May 20, 2020 and December 19, 2021 and were required to search and document their efforts. People were assigned by birthday-based randomization: about half to a control group and about one quarter to each of two treatment conditions. The researchers excluded some registered birthdays that were not plausibly random for immigrants from nine countries and reported that the retained groups were well balanced on register characteristics.
The treatments lasted for the first six months of an unemployment spell. A person in either treatment group could receive up to six monthly emails, and messages stopped if they found a job. The control group received no study emails, though they continued to receive ordinary communications from the Public Employment Service. Caseworkers did not know about the experiment, reducing the risk that they would consciously change how they treated recipients. The comparison was thus between assignment to a study-email package and no study email within a real benefits and monitoring regime.
That last qualification is important. The study was not a laboratory test in which only one phrase changed. Both email types included practical job-search advice and links. The control condition did not receive an otherwise identical neutral message, because the researchers found it difficult to create one without also trying to motivate recipients. The randomized estimates therefore capture the effect of receiving the complete supportive or controlling package relative to the study control, not the isolated effect of a single word.
The design nevertheless makes the comparison informative. The two treatments were sent by the same agency, addressed the same reporting cycle, and were kept as similar as possible in practical content and length. Caseworkers did not know which clients received which messages, so the estimated difference was not created by a deliberate change in counseling. The treatments also differed in the reason they gave for the same broad activity: one linked action to choice, competence, and support; the other linked it to obligation and sanctions. That is enough to test whether motivational framing adds something beyond ordinary contact with the agency, while still requiring caution about what exactly caused any effect. If the controlling arm increases a report but not applications, the evidence points to a separation between compliance and search. If the supportive arm changes applications, that is a treatment-package result occurring within a strict institutional relationship, not a general verdict on the value of encouragement.
Two message schemes entered the same monthly cycle
The researchers used Self-Determination Theory to give the two treatment arms different motivational targets. The theory distinguishes autonomous motivation from controlled motivation. Autonomous motivation means that a person endorses an action because it is interesting, meaningful, personally relevant, or connected to a self-chosen goal. Controlled motivation means acting under pressure, whether from an external demand or from internal feelings such as guilt, shame, or obligation.
The supportive messages tried to strengthen autonomous motivation by addressing autonomy, competence, and relatedness. They used language of choice—what a job seeker “can” or “may” do—and explained why reporting or search activities could be useful. They expressed confidence in the recipient’s ability, acknowledged the frustration and loss of confidence that repeated rejection can cause, and adopted a more personal tone. A typical message thanked the recipient for reporting, connected the report to the support the service could provide, and described several ways to look for a suitable job or education.
The controlling messages pursued the opposite motivational route. They emphasized that activity reporting was a requirement, that the recipient was expected to search and accept suitable offers, and that breaking the rules could lead to a warning or suspension of benefits. The wording used terms such as “must,” “required,” and “obliged.” The tone was more formal and impersonal, referring to the Public Employment Service and the rules rather than primarily to the recipient’s goals.
The contrast was intentional but not careless. The messages were kept similar in length, practical advice, timing, subject lines, and sender. They were drafted, translated into Swedish, reviewed by employment-service staff and labor-market experts, back-translated, and tested in a pilot. Those checks make it less likely that the two arms differed merely because one was confusing or badly written. They do not prove that every recipient experienced the intended psychological state. The intermediate survey did not detect statistically significant changes in measured autonomous or controlled motivation, although the authors point to limited statistical power and the difficulty of measuring these concepts.
The first observable transition was attention. Across two cohorts, 11,102 of 15,436 messages were opened, an overall rate of 72%. The first email was opened by about 75% of recipients in both treatment conditions, so the initial opportunity to encounter the two schemes was comparable. Subsequent engagement differed: later open rates were higher in the controlling condition, and conditional clicks on embedded information links were also higher there. These figures show that the message content could affect how recipients engaged with later emails. They do not show that recipients agreed with the message, changed their underlying motivation, or searched more effectively.
The next transition was reporting. Both treatments increased the share of monthly activity reports submitted. Across the first six months, the controlling emails raised reporting by 1.13 percentage points relative to the control group, while the supportive emails raised it by 0.76 percentage points. The control-group mean was 45.6% over that period. The response was strongest for the first report and smaller for reports later in the spell. That decay is consistent with the emails making a recurring formal deadline salient, especially when recipients first entered the intervention, although it does not by itself identify the psychological process.
The difference between the message schemes at this stage also fits their wording. The controlling messages explicitly highlighted the reporting obligation, so a stronger early compliance response was plausible. The supportive messages still thanked recipients for reporting and explained why the report could help the service understand their situation, so they too could increase submission. The important point is that both schemes moved the record the agency could see. The test of effective search came later.
That first-stage result should not be dismissed as a meaningless paperwork effect. The report was the institution’s main recurring window onto search, and failing to submit it could put benefits at risk. A reminder that prevents a missed report may protect a person from an avoidable administrative failure. But the same institutional importance makes the measure easy to overinterpret. The report records that an activity was declared; it does not necessarily reveal how much time the person spent searching, whether an application was well matched, or whether the person changed the occupation or employer being targeted. A system can therefore become better at observing compliance without becoming better at producing employment.
The timing of the response adds another clue. The first report showed a much larger treatment response than later reports, while the controlling treatment’s advantage over the supportive treatment was clearest early in the sequence. That pattern is consistent with an intervention making a recurring deadline newly salient, rather than steadily transforming a person’s reason for searching. It is not a definitive test of the reminder explanation, and the survey measures of motivation are limited. Still, the timing tells us why the reporting result should be read as evidence about an immediate administrative transition, not as a long-term measure of changed search capacity.
After the reporting response, the two paths separated from the intervention’s intended prediction. The controlling treatment had no statistically significant effect on the number of formal job applications per month during months 2–7, one of the primary outcomes. It also had no significant effect on leaving unemployment within seven months, the other primary outcome, or on the related secondary job-finding measures. The estimates were small enough that the authors regard low statistical power as an unlikely explanation for the pattern. In their interpretation, pressure may have reminded people to complete the formal report without changing the search effort represented by applications.
The supportive treatment moved in the wrong direction on some search measures. It reduced applications by 0.128 per month during months 2–4 and by 0.094 per month during months 2–7. The longer-window estimate was about a 1.1% reduction from the control mean of 8.286 applications per month. Job finding within seven months was not significantly different from the control group, but job finding within four and twelve months was slightly lower; the twelve-month reduction was about 0.4 percentage points and statistically significant. The paper found no systematic improvement in job-search quality or job quality for either treatment.
This sequence produces a result that is surprising only if reporting and search are treated as the same behavior. The emails had a measurable first-stage effect. The controlling version was particularly effective at eliciting a response to a formal requirement. But neither treatment produced the expected improvement in the applications or job-finding outcomes that would make the reporting response substantively valuable. The supportive version even produced a modest adverse effect in selected measures. The estimates describe this Swedish intervention in this Swedish relationship; they do not establish that all controlling messages merely remind, or that supportive communication generally harms job seekers.
The unresolved issue is therefore not whether the messages were inert. They were not. It is what recipients understood the messages to mean inside an already monitoring-oriented institution, and whether the intervention was aimed at the limiting problem. The next interpretation must weigh the possibility that soft language conflicted with the surrounding relationship, that pressure was redundant or harmful for some people, and that the intervention tried to alter motivation when the more important obstacle lay elsewhere. The Swedish result becomes useful once the size of the first-stage response is kept separate from the search outcome it failed to produce.