Types of studies

We will include RCTs, quasi‐RCTs (in which the method used for the allocation of participants is not random, such as alternate allocation, allocation by date of birth, or day of the week), cluster‐randomised trials (randomisation of a group of people such as a work group or workplace rather than randomisation of the individual) and cross‐over RCTs. We will include only studies conducted in the real workplace, excluding studies conducted under laboratory conditions. We will include studies reported as full‐text, those published in abstract form only and unpublished data.

Types of participants

We will include trials enrolling healthy adult workers (aged 18 years or above).

Types of interventions

We will include studies that have evaluated one or more of the following types of work‐break interventions.

• Changes in the frequency of work breaks

  • Intervention: higher (i.e. > 3 per day)

  • Control: low (i.e. ≤ 3 per day)

• Changes in the duration of work breaks

  • Intervention: short (i.e. ≤ 15 minute) or micro (i.e. ≤ 1 minute)

  • Control: 15 to 30 minutes (15‐minute breaks during the morning and afternoon shifts, 30‐minute breaks halving the 8‐hour working day; see the study by Galinsky 2000 for a discussion about conventional work‐break schedules)

• Changes in the type of work break

  • Intervention: active or cognitive

  • Control: passive

These work‐break interventions may be tested or applied in work situations. To be included, a study has to compare the intervention with a control (no intervention or another type of work‐break intervention).

Types of outcome measures

We will include studies that have assessed the effect of a work‐break schedule on at least one of the following primary outcomes.

Electronic searches

We will systematically search for all eligible published and unpublished trials. We will impose no restrictions on language of publication, which means we will arrange for the translation of key sections of foreign‐language studies or attempt to find native speakers or people who are proficient in the publications’ language to assist with translating these studies for potential inclusion.

Our search strategy for the MEDLINE database is shown in (Appendix 1); this search strategy will be adjusted to the formats of other databases, when necessary. We will search the following electronic databases from inception to present to identify potential studies that are already published:

• Cochrane Central Register of Controlled Trials (CENTRAL) (Wiley Online Library);

• MEDLINE (PubMed) (Appendix 1);

• Embase (embase.com) (OVID);

• CINAHL (EBSCO);

• PsycINFO (ProQuest) (OVID);

• SCOPUS (Elsevier);

• Web of Science (Thomson Reuters).

We will also conduct a search for unpublished trials in ClinicalTrials.gov (ClinicalTrials.gov) and the World Health Organization International Clinical Trials Registry Platform (who.int/ictrp/en/).

Searching other resources

We will check the reference lists of all primary studies included and those of review articles for additional references. We will contact experts in the field to identify additional unpublished studies.

Selection of studies

Will will follow a two‐stage plan for selecting studies for inclusion in the review. In stage one, two review authors (TL, BS) will independently screen the titles and abstracts of the identified citations, and obtain the full text of all studies that at least one author deems potentially eligible. In stage two, two review authors (TL, BS) will independently assess the full publication for eligibility and compare their results. We will tabulate the characteristics of excluded studies in the ‘Characteristics of excluded studies’ table. We will resolve any disagreement through discussion or, if required, by consulting a third review author (MR). We will identify and exclude duplicates, and collate multiple reports of the same study so that each study rather than each report is the unit of interest in the review. We will record the selection process in sufficient detail to complete a PRISMA flow diagram (Moher 2009).

When our systematic searches identify studies conducted by one of the review authors, we will avoid a conflict of interest by having all decisions concerning inclusion and exclusion made by review authors who were not involved with the study.

Data extraction and management

We will input study characteristics and outcome data into a data collection form that we will pilot on at least one study in the review. One review author (TL) will extract the following study characteristics from the included studies.

• General: authors and year of publication.

• Methods: study design, total duration of study, study location, study setting, withdrawals, and date of study.

• Participants: number, randomisation, mean age or age range, sex/gender, occupation, health status, inclusion criteria, and exclusion criteria,

• Interventions: description of intervention, comparison, duration, intensity, content of both intervention and control condition, co‐interventions, and washout period including the length between the application of the intervention and the control or vice versa (applicable to cross‐over RCTs).

• Outcomes: description of primary and secondary outcomes specified and collected, and time points reported.

• Notes: funding for trial, and notable conflicts of interest of trial authors.

Two review authors (TL, BS) will independently extract outcome data from the included studies. We will note in the ‘Characteristics of included studies’ table if outcome data was not reported in a usable way. We will resolve disagreements by consensus or by consulting a third review author (MR). One review author (TL) will transfer data into Review Manager 5 (RevMan 2014); a second review author (BS) will spot‐check study characteristics for accuracy against the trial report. Should we decide to include studies published in a language in which our author team is not proficient, we will arrange for a native speaker or someone sufficiently proficient in the language to fill in the data extraction form for us.

Assessment of risk of bias in included studies

Two review authors (TL, BS) will independently assess the risk of bias in each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreements through discussion or by involving a third review author (MR). We will assess the risk of bias according to the following domains:

1. random sequence generation;

2. allocation concealment;

3. blinding of participants and personnel;

4. blinding of outcome assessment;

5. incomplete outcome data;

6. selective outcome reporting;

7. carry‐over;

8. other bias.

We will grade each potential source of bias as high, low or unclear, and provide a quote from the study report together with a justification for our judgement in the ‘Risk of bias’ table. We will summarise the ‘Risk of bias’ judgements across different studies for each of the domains listed. We will consider blinding separately for different key outcomes where necessary (e.g. for the assessment of blinding of outcomes, the risk of bias for a diagnosis of musculoskeletal disorder may be very different than that for a participant‐reported discomfort scale). Where information on risk of bias relates to unpublished data or to correspondence with a trialist, we will note this in the ‘Risk of bias’ table.

We consider random sequence generation, allocation concealment, incomplete outcome data, selective outcome reporting, and carry‐over (applicable to cross‐over RCTs) to be key domains. We will judge a study to have a high risk of bias when we judge one or more key domains to have a high risk of bias. Conversely, we will judge a study to have a low risk of bias when we judge all key domains to have a low risk of bias.

Measures of treatment effect

We will enter the outcome data for each study into the data tables in RevMan 2014) in order to calculate the treatment effects. We will use risk ratios rather than odds ratios for dichotomous outcomes, hazard ratios for time‐to‐event data, and mean differences or standardised mean differences for continuous outcomes, or other type of data as reported by the authors of the studies. If only effect estimates and their 95% confidence intervals or standard errors are reported in studies, we will enter these data into RevMan 2014 using the generic inverse variance method. We will ensure that higher scores for continuous outcomes have the same meaning for each outcome, explain the direction to the reader, and report where the directions were reversed if necessary. When the results cannot be entered in either way, we will describe them in the ‘Characteristics of included studies’ tables, or enter the data into ‘Additional tables’.

For cross‐over trials that report continuous outcomes, we will use the paired analysis as reported by the authors and include the mean difference between the intervention and control conditions and its standard error into RevMan 2014 using the generic inverse variance method for calculating the effect estimate. In cases where the authors have not reported paired analysis, we will conduct the analysis ourselves based on the reported or imputed correlation between the outcomes of the intervention and the control conditions, as advised in Chapter 16 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). For dichotomous outcomes, we will also use the paired analyses reported by the authors, but if these are missing we will calculate odds ratios and adjust their confidence intervals for the paired nature of the data according to Elbourne 2002, based on the reported or imputed correlation between the outcomes of the intervention and the control conditions.

Unit of analysis issues

For studies that employ a cluster‐randomised design and that report sufficient data to be included in meta‐analysis but do not make an allowance for the design effect, we will calculate the design effect based on a fairly large assumed intracluster correlation of 0.10. We consider 0.10 to be a realistic estimate based on intracluster correlation values typically seen in cluster RCTs (Campbell 2001). For the calculations, we will follow the methods as stated in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

Dealing with missing data

We will contact investigators or study sponsors in order to verify key study characteristics and obtain missing numerical outcome data where possible (e.g. when a study is published in abstract form only). Where this is not possible and the missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results using sensitivity analysis. If we are unable to obtain these data even after contacting authors, we will list such studies under ‘Studies awaiting classification’.

If numerical outcome data, such as standard deviations or correlation coefficients, are missing and cannot be obtained from the authors, we will calculate them from other available statistics, such as P values, according to the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

Assessment of heterogeneity

We will assess the clinical homogeneity of the results of the included studies based on similarity of population, intervention, outcome and follow‐up. We will follow the algorithm provided by (Verbeek 2012).

We will consider populations as similarwhen they are exposed to high physical demands (i.e. industrial or factory work) and low physical demands (i.e. computer or social work) .

We will consider interventions as similar when they belong to one of three intervention categories as defined in the section 'Types of interventions'. Interventions that address a low or high work‐break frequency will be considered different; interventions that address a long, short or micro work‐break duration will be considered different; and interventions that address a passive, active or cognitive work‐break type will be considered different.

We will consider any method used to record participant‐reported complaints (e.g. Borg scale, VAS, questionnaires) and participant‐reported workloads (e.g. the TLX questionnaire) to be similar. We will consider any standardized questionnaire used for the assessment of work performance and productivity (e.g. Health and Work Performance Questionnaire) to be similar. We will consider any objective technique related to workload changes (e.g. force, endurance time, muscle activity) to be similar.

We will regard short‐term (up to six weeks), medium‐term (from six weeks to up to six months) and long‐term (more than six months) follow‐up times to be different.

We will assess heterogeneity by the visual inspection of forest plots and by using the I² statistic. We will then quantify the degree of heterogeneity (Higgins 2011), and consider an I² value greater than 75% to represent considerable heterogeneity. In the presence of substantial heterogeneity and a sufficient number of studies, we will explore possible causes by conducting prespecified subgroup analyses.

Assessment of reporting biases

If we are able to pool seven or more trials in any single meta‐analysis, we will assess publication bias by funnel plots and examine funnel plot asymmetry using the Egger’s test (Higgins 2011).

Data synthesis

We will pool data from studies judged to be clinically homogeneous using RevMan 2014. If more than one study provides usable data in any single comparison, we will perform meta‐analyses. We will use a random‐effects model to pool the results of studies (Borenstein 2009). When I² is higher than 75% we will not pool the results of studies in meta‐analysis.

We will include 95% confidence intervals for all estimates. We will narratively describe skewed data reported as medians and interquartile ranges.

Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons are combined in the same meta‐analysis, we will halve the control group to avoid double‐counting.

Subgroup analysis and investigation of heterogeneity

When data allow, we plan to carry out the following subgroup analyses for each outcome.

1. Type of intervention (if possible, we will compare studies that changed the frequency of work breaks with studies that changed the duration of work breaks and with studies that changed the type of work breaks).

2. Age (if possible, we will compare studies conducted in participants aged 18 to 40 years with studies where all participants are aged 41 years and older).

3. Sex (if possible, we will compare males with females).

4. Type of work task (if possible, we will compare industrial or factory work, such as assembling, with computer work and social work, such as nursing and garbage collecting).

We will use the Chi² test to test for subgroup interactions in RevMan 2014.

Sensitivity analysis

We will perform a sensitivity analysis to investigate whether our findings could be affected by the high risk of bias of some of the included studies. We will consider studies to be at high risk of bias if random sequence allocation, allocation concealment, incomplete outcome data, selective outcome reporting, or carry‐over (applicable to cross‐over RCTs) are rated as unclear or high risk, and exclude these studies from the analysis.