Types of studies

We will include randomised controlled trials (RCTs) and cluster RCTs, as well as such non‐randomised controlled trials as controlled before‐after (CBA) studies and interrupted time‐series (ITS) studies. We will include studies reported as full text, those published as abstract only, and unpublished data.

In RCTs, there is the risk of contamination, where a HCW randomised to an intervention may influence a co‐worker randomised to a control group to also take vaccination. A cluster RCT, in which groups of individuals are randomly allocated to an intervention or non‐intervention group, is one way to avoid this contamination.

In occupational safety and health, there is no culture of randomised controlled studies to evaluate interventions. This makes RCTs less likely, and so we will also include CBA studies. In accordance with the Cochrane Effective Practice and Organisation of Care (EPOC) Group, we will exclude studies with only one intervention or control site (EPOC), because with such studies, the intervention (or comparison) can be confounded by study site, making it difficult to attribute any observed differences to the intervention rather than to other site‐specific variables. We will therefore only include cluster RCTs and CBA studies with at least two intervention sites and two control sites (EPOC).

We will also consider ITS studies, which observe the effect of an intervention over time. EPOC defines ITS studies as studies in which the outcome has been measured at least three times before and three times after the intervention (EPOC; Ramsay 2003). For vaccination uptake especially, we expect data to be collected over time.

Types of participants

We will include HCWs (such as nurses and midwives, doctors, nursing and medical students, other health professionals, cleaners, porters or volunteers) who have regular contact with patients in hospitals, clinics, or primary care centres.

We will include studies in which the intervention has been targeted to either the entire workforce or select employees (for example, just nurses).

Where a study includes a combination of populations, we will include only studies that have 50% or more HCWs, unless the results for HCWs are reported separately.

Types of interventions

We will consider all types of interventions intended to increase the uptake in HCWs of the following recommended vaccinations: pertussis; influenza; measles, mumps and rubella (MMR); varicella; hepatitis B; hepatitis A; and Bacillus Calmette–Guérin (BCG).

We will study the following four groups of interventions:

1. Policy or legislation that:

• makes recommended HCW vaccinations mandatory and requires declination statements for HCWs who refuse vaccination indicating that they understand the rationale for offering the vaccine and the risks of refusal;

• requires HCW screening on commencement of employment; or

• requires HCW screening at regular time points.

2. Incentives

• Individual HCW incentives such as financial or food rewards (for example, free coffee or money bonus at the individual level if a person is vaccinated).

• Group HCW incentives such as financial or food rewards (for example, free coffee or funding at the group level, such as a ward or department, if a certain level of uptake is achieved).

• Organisational incentives such as additional funding at an institutional level if a certain level of uptake is achieved.

3. Improving access to vaccinations:

• through after‐hours clinics, mobile vaccination trolleys, or making them available at the workplace;

• by providing them free of charge to HCWs.

4. Educational interventions

• Posters, pamphlets, or staff badges worn following immunisation for raising awareness of policy or programme, recommendations for HCWs, or risks and benefits of vaccinations.

• Reminder interventions, for specific vaccinations or for all those recommended.

We will compare interventions to no intervention or to a control intervention (an intervention not thought to promote immunisation in HCWs) or an alternative intervention for promoting immunisation.

Where an intervention has multiple components, such as an intervention with a policy and educational component, we will compare them with other interventions that share the predominant component but we will separate them in subgroup analysis.

When we encounter interventions other than those listed above, we will make additional categories and comparisons.

Types of outcome measures

Electronic searches

We will conduct a systematic literature search to identify all published and unpublished trials eligible for inclusion in this review. We will adapt the search strategy we developed for PubMed (see Appendix 1) for use in the other electronic databases. We will identify potential studies in all languages, assessing non‐English‐language papers with the help of Google translate or a native speaker and using a native speaker to assist with data extraction.

We will search the following electronic databases from inception to present for identifying potential studies:

• Cochrane Central Register of Controlled Trials (CENTRAL)

• MEDLINE (Appendix 1)

• EMBASE

• PsycINFO (ProQuest)

• NIOSHTIC (OSH UPDATE)

• NIOSHTIC‐2 (OSH UPDATE)

• HSELINE(OSH UPDATE)

• CISDOC (OSH UPDATE)

• CINAHL

We will also conduct a search of ClinicalTrials.gov (www.ClinicalTrials.gov) and the World Health Organization trials portal (www.who.int/ictrp/en/).

Searching other resources

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

Selection of studies

All review authors will independently screen titles and abstracts for inclusion in pairs and they will code them as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. Review authors in pairs will screen the retrieved full‐text study reports/publication, identifying studies for inclusion and identifying and recording reasons for exclusion of the ineligible studies. Any disagreements will be resolved through discussion with all review authors. 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 and 'Characteristics of excluded studies' table.

Data extraction and management

We will use a data collection form for study characteristics and outcome data that has been piloted on at least one study in the review. One review author (JT) will extract study characteristics from included studies. We will extract the following study characteristics.

1. Methods: study design, total duration of study, study location, study setting, withdrawals/dropouts, and date of study.

2. Participants: N, mean age or age range, sex, current vaccination rates, inclusion criteria, and exclusion criteria.

3. Interventions: description of intervention, comparison, duration, intensity (for example, amount of education provided to participants), content of both intervention and control, and co‐interventions. If the intervention is very complex and consists of many elements, we will report the contents in an additional table.

4. Outcomes: description of primary and secondary outcomes specified and collected, and at which time points reported.

5. Notes: study funding and notable conflicts of interest of study authors.

Two review authors (JT and JC) will independently extract outcome data from included studies. We will note in the 'Characteristics of included studies' table if outcome data were not reported in a usable way. We will resolve disagreements by consensus or by involving a third person (HM). One review author (JT) will transfer data into Review Manager (RevMan 2014) file. We will double‐check that data are entered correctly by comparing data presented in the systematic review with the study reports. A second review author (JC) will spot‐check study characteristics for accuracy against the study report.

Assessment of risk of bias in included studies

Two review authors (JT and JC) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreements by discussion or by involving another author (HM).

We will assess the risk of bias of selected RCTs and cluster RCTs according to the following domains, and 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 judgment 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. Where information on risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the 'Risk of bias' table.

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. other bias

For controlled before‐after studies, we will use the validated instrument for appraising risk of bias of controlled before‐after studies by Downs 1998. The instrument has been shown to have good reliability and internal consistency and validity. The list consists of five different subscales: reporting, external validity, bias, confounding, and power). We will only use the combined score on the two internal validity subscales (bias and confounding) to judge the quality of the included controlled before‐after studies. We will use an arbitrary cut‐off score of 50% of the maximum attainable score of the internal validity scale to discern low from high risk of bias. We will modify the criteria for risk of bias so that they fit the risk‐of‐bias tool as implemented in RevMan (RevMan 2014) by changing them from 0 and 1 to high, low, and unclear.

We will also check for relevant and considerable baseline differences between control and intervention groups based on healthcare facility size, workforce composition, and vaccination rates.

For ITS studies, we will use the quality criteria developed by the Cochrane Effective Practice and Organisation of Care Group (EPOC). The quality assessment for ITS designs consists of:

1. protection against secular changes (three items);

2. protection against detection bias (two items);

3. completeness of data set (one item); and

4. reliable primary outcome measures (one item).

We will answer each item as 'done', 'not clear', or 'not done'.

When considering intervention effects, we will take into account the risk of bias for the studies that contribute to that outcome.

Measures of treatment effect

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

For ITS studies, we will extract data from the original papers and re‐analyse them according to the recommended methods for analysis of ITS designs for inclusion in systematic reviews (Ramsay 2003). For ITS studies, we will use the standardised change in level and change in slope as effect measures.

Unit of analysis issues

For studies that employ a cluster‐randomised design and that report sufficient data to be included in the 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 base this assumption of 0.10 being a realistic estimate by analogy on studies about implementation research (Campbell 2001). We will follow the methods stated in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) for the calculations.

Dealing with missing data

We will contact investigators or study sponsors to verify key study characteristics and to obtain missing numerical outcome data where possible (for example, when a study is identified as abstract 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 by a sensitivity analysis.

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 included studies based on similarity of population, intervention, vaccine antigen protected against, outcome, and follow‐up. We will consider populations as similar when they are the same professional group, such as physicians or nurses only or the entire HCW workforce for a healthcare facility. We will consider the effects of policy changes, incentives, improving access to vaccination, and educational interventions to be different.

Interventions may have different effects for specific vaccine‐preventable diseases. This is based on distinct differences in the behaviour or attitudes that drive the vaccination for different diseases. However, we will consider the effect of interventions first to be generic and assess this assumption by subgroup analysis.

We will regard follow‐up times of immediate (within the same calendar year or season of intervention, medium (one to five years), and long term (greater than five years) as different.

We will use the I² statistic to quantify heterogeneity among the trials in each analysis. If we identify substantial heterogeneity, we will report it and explore possible causes by prespecified subgroup analysis.

We will regard 50% or above as a substantial level of heterogeneity, recognising that there is uncertainty in the I² measurement when there are few studies in a meta‐analysis (Higgins 2011). We will adopt the values for interpretation proposed in the Cochrane Handbook for Systematic Reviews of Interventions (0% to 40%: might not be important; 30% to 60%: may represent moderate heterogeneity; 50% to 90%: may represent substantial heterogeneity; 75% to 100%: considerable heterogeneity) (Higgins 2011). We will also test for statistical heterogeneity by means of the Chi² test as implemented in the forest plot in RevMan 5.3 (RevMan 2014), and we will use a significance level of P value < 0.10 to indicate whether there is a problem with heterogeneity. If we identify substantial heterogeneity, we will report it and explore possible causes by prespecified subgroup analysis.

Assessment of reporting biases

If we are able to pool more than 10 trials in any single meta‐analysis, we will create and examine a funnel plot to explore possible small‐study biases.

Data synthesis

We will pool data from studies judged to be clinically homogeneous using RevMan 5.3 software (RevMan 2014), but we will present results separately for randomised studies, controlled before‐after studies, and interrupted time‐series studies.

If more than one study provides usable data in any single comparison, we will perform meta‐analysis. When studies are statistically heterogeneous, we will use a random‐effects model; otherwise we will use a fixed‐effect model. When using the random‐effects model, we will conduct a sensitivity check by using the fixed‐effect model to reveal differences in results. We will include a 95% confidence interval for all estimates.

For interrupted time‐series studies, we will perform separate meta‐analyses for level and slope using the generic inverse variance method.

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 (for example, intervention A versus control and intervention B versus control) are combined in the same meta‐analysis, we will halve the control group to avoid double counting.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses:

1. Intervention category subtype;

2. Healthcare worker professional group, i.e. nurses, physicians, other medical staff; and

3. Disease targeted, e.g. hepatitis B, seasonal influenza, pertussis.

We will use the following outcome in subgroup analyses:

1. Number of staff vaccinated

Sensitivity analysis

We will perform sensitivity analysis defined a priori to assess the robustness of our conclusions. This will involve:

1. omitting studies judged to have a high overall risk of bias using the 50% arbitrary cut‐off score as described in Assessment of risk of bias in included studies; and

2. if the random‐effects model is used, we will conduct a sensitivity check by using the fixed‐effect model to reveal differences in results.