Health Promoting Work Schedules: The Effect of Abolishing Quick Returns

Summary

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Aims This is a two-arm cluster randomized controlled trial that assesses the consequences of a shift work schedule without quick returns for six months, compared to a schedule that include quick returns. First, we will examine any differential change in sickness absence, during the six-month interve...

Aims This is a two-arm cluster randomized controlled trial that assesses the consequences of a shift work schedule without quick returns for six months, compared to a schedule that include quick returns. First, we will examine any differential change in sickness absence, during the six-month intervention period. Second, we will examine if there are differential changes in sleep and functioning, physical and mental health, work-related accidents, and turnover intention, among others. Third, we will investigate if individual characteristics associated with shift work tolerance including sex, age, personality and subjectively reported sleep need will moderate the negative effects of quick returns on the primary and secondary outcomes. Finally, the study will investigate if individual factors like satisfaction with work schedule, job satisfaction, job engagement and work-family interference will moderate the negative effects of quick returns on the primary and secondary outcomes. Research design A cluster randomized controlled trial comparing a work schedule abolishing quick returns (intervention) with that of a work schedule maintaining a normal amount of quick returns (control) will be conducted. The clusters represent hospital units that are randomly selected to receive (or not receive) the intervention. 'Normal amount of quick returns' refer to that which is the common practice at the respective hospital unit in recent years (i.e., when no explicit changes have been made to the work schedule), which means that the total number of quick returns at the unit will vary from 329-2356 per year. The hospital units were randomized to one of the two conditions in September 2020, of which the autumn of 2020 was spent planning the shift schedule for 2021 (i.e., removing quick returns for the intervention group and leaving quick returns untouched for the control group), with the intervention period commencing from February/March 2021 for most units. The intervention period in this study is six calendar months. Most units in this trial start the intervention period in February/March 2021, but some units will, for practical reasons, start the intervention period in the second half of the rotation year, i.e. from August/September 2021. The primary outcome is sickness absence retrieved from the local records kept by the hospital (including short- and long-term sick leave). The baseline measurements will be sickness absence from the year preceding the intervention, which for each individual participant will be matched on duration and season to that of the intervention period. Sickness absence data will be retrieved from the local records kept by the hospital.(Vedaa, Pallesen et al. 2017) This record includes information about the date of any absence of the individual employee, implying that it includes information about both short- and long-term sickness absence. Further, these data include information on whether the absence is self-certified or whether it is certified by a physician, whether the absence is due to a sick child of whom the employee has caretaker responsibility of, and whether the absence is due to COVID-19 related issues (e.g., quarantine). The use of register data will not require individual consent. However, a consent-based part of the trial will also be conducted, in which secondary outcome measures will be collected via questionnaire at baseline and six-month follow-up. All employees (n ? 2700) at the randomized units will be asked to complete a digital questionnaire made available via the hospital's internal website. Baseline assessment will occur the month preceding the intervention period, and follow-up assessment will occur the last month of the intervention period. A subsample (n ? 70) will be asked to objectively record their sleep with advanced radar technomogy (Somnofy™) and subjectively with sleep diaries for ?1 week at the baseline and follow-up assessments, respectively. Participants and procedure Recruitment This trial is carried out in close collaboration with the human resources department at Haukeland University Hospital. All hospital care units that have 24-hour staffing at hospital will be randomized, in which all healthcare workers working shifts will be included, with the exception of physicians. Physicians will not be included since they often have a different shift schedule and compensation scheme compared to the other occupational groups. Hereinafter, 'all employees' refer to all healthcare workers engaged in shift work at the randomised hospital units, with the exception of physicians. All employees (n ? 2700) at the randomized hospital units will be asked to complete a questionnaire prior to and at the end of the intervention period. Recruitment for this part of the trial will take place via the hospital's internal website. Researchers and human resources personnel at the hospital will attend staff meetings at all included units to inform about the research project and encourage participation. A subsample of n ? 70 randomly selected employees (evenly distributed from the intervention and the control units) will be recruited for the sleep monitoring section of the trial. Randomisation Eligible hospital units were randomized to one of the two conditions based on stratification on unit size and total number of quick returns in the unit during the last year (range: 329-2356). The randomization procedure will follow a 1:1 ratio. Sample size The necessary sample size (assuming a power of .80 and significance level of .05) was calculated to be 448 participants in each condition. This calculation was based on the mean values of sickness absence days per month (0.9 days, SD=1.6), as reported in Vedaa et al.(Vedaa, Pallesen et al. 2017). In the present trial, we will also examine potential moderators and mediators in exploratory analyses, which will require an appreciably larger sample size. For the primary outcome measure in this trial (sickness absence from register data), we will have an expected sample size of ? 2700. This includes all employees (who work >=50 percent of full time equivalent) in the randomized hospital units and is considered sufficient for all conceivable purposes of this trial. Data analysis plan All analyses will be conducted based on the intention-to-treat population, unless otherwise stated. To examine the effects of a shift schedule abated of quick returns on primary and secondary outcomes, the observed rates or scores will be analysed by means of latent growth models (or other equivalent models such as generalized linear mixed models). The observed rates or scores before and during the intervention period will be modelled by a random intercept and a fixed slope. The effect of the intervention will be estimated by using the group variable (intervention vs. control) as a predictor of the slope. Between-group effect sizes (Cohen's d) will be calculated by dividing the mean difference in estimated change in scores from baseline to the follow-up assessment by the pooled SD at baseline. Robust maximum likelihood will be used as the estimator, providing unbiased estimates under the assumption of data being missing at random,(Enders 2010) which might be partly met through the inclusion of baseline scores to the model. The primary outcome measure in this trial is sickness absence data retrieved from the register at the hospital, in which we expect no missing data. However, it is reasonable to expect some missing data on the secondary outcome measures, as data are collected through questionnaire or via the sleep radar. As some data for the follow-up questionnaire and sleep radar assessment will be missing not at random, the robustness of the results under the missing-at-random assumption will be tested by sensitivity analyses in which the missing scores at follow-up will be replaced by baseline values for each respective individual. These sensitivity analyses will only be performed on selected variables depending on the focus in the respective article. The intention-to-treat analyses may be accompanied by selected per-protocol analyses in which we, based on payroll data, define a group that has completely abolished or had a satisfactory reduction in the number of quick returns over the intervention period. The primary outcome of sick leave will mainly be analysed in terms of the total number of sickness absence days and periods (spells) for a given period before compared to during the intervention period.(Vedaa, Pallesen et al. 2017) The models of sickness absence will take into account the zero inflation in this type of data. Other operationalisations of sickness absence might also be considered in accordance with recommendations in the literature.(Hensing, Alexanderson et al. 1998) For a further investigation of the sickness absence data, we will consider the use of other models where we treat time differently. For example, we will consider models where we look at the time to the first sick leave episode for the two intervention groups, with a time-dependent covariate for the number of quick returns (ie, a variable that increases by 1 each time the person has a quick return). Another possibility is to say that participants start at "0" every time the person has a quick return, and to measure time from the last quick return to the first subsequent sick leave episode, while adjusting for repeated observations with e.g. robust variance estimate (the non-quick return group will then only be followed from the start of the intervention, given that they in fact have no quick returns). Another option is to set up a model for time from sick leave to return to work. Since the introduction of a work schedule without quick returns may entail an alternative schedule with an increase in other undesirable characteristics (e.g., more consecutive evening shifts), we will consider conducting analyses that adjust for such characteristics. Mediator and moderator analyses will be performed for exploratory purposes, based on the basic principle for such analyses in randomised controlled trials as described by others ((e.g., Kraemer, Wilson et al. 2002)). For example, some of the data collected on demographics, sleep-related personality traits (rCTI and MEQ), mental health, among others, can be used to examine factors that may moderate the impact of the intervention. References Enders, C. K. (2010). Applied missing data analysis. New York, NY, US, Guilford Press. Hensing, G., et al. (1998). "How to measure sickness absence? Literature review and suggestion of five basic measures." Scandinavian journal of public health 26: 133-144. Kraemer, H. C., et al. (2002). "Mediators and moderators of treatment effects in randomized clinical trials." Archives of General Psychiatry 59: 877-883. Vedaa, Ø., et al. (2017). "Short rest between shift intervals increases the risk of sick leave: a prospective registry study." Occupational and Environmental Medicine 74: 496-501.

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