Types of studies

Due to the complex nature of the intervention, which is applied at the group level in work situations rather than at the individual level, randomised controlled trials (RCTs) are less feasible, which is one of the major reasons for the inclusion of non‐randomised studies in Cochrane Reviews (Ijaz 2014). Therefore, we will include also other study designs beyond the RCT. We will include comparative studies that are commonly performed in this field, that is, historically controlled studies and cohort studies. We will also include interrupted time‐series, controlled‐before‐and‐after (CBA), and case‐control studies. This is because interrupted time‐series may account for time trends in improvement of practices and CBA studies may account for any interim changes in policies. We will include case‐control studies because the outcomes following exposure are rare.

Types of participants

We will include studies conducted on adult healthcare staff (aged 18 years or above) involved in the preparation, transport, delivery, administration, and disposal of waste of infusional hazardous drugs. We will also consider healthcare organisations in which healthcare staff are exposed to infusional hazardous drugs as participants with regards to outcomes such as surface contamination and aerosol contamination.

Types of interventions

We will include trials that have evaluated the effectiveness of closed‐system drug‐transfer of infusional hazardous drugs (e.g. PhaSeal system and ChemoClave system), with safe handling of infusional hazardous drugs (e.g. including Class II biological safety cabinet, isolator, and personal protective equipment) versus safe handling alone. We will accept any device described as a closed‐system drug‐transfer device by the manufacturer. We will include trials with any cointerventions provided they are not part of the randomised treatment or have been applied equally in both arms in non‐randomised studies.

Types of outcome measures

Electronic searches

We will conduct a systematic literature search to identify all published and unpublished trials that can be considered eligible for inclusion in this review. We will adapt the search strategy we developed for MEDLINE (see Appendix 1) for use in the other electronic databases. We will impose no restrictions on language of publication. We will translate the key sections of potentially eligible non‐English language papers to assess them fully for potential inclusion in the review as necessary.

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

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

• MEDLINE (OvidSP) (Appendix 1);

• Embase (OvidSP);

• NIOSHTIC (OSH‐UPDATE);

• NIOSHTIC‐2 (OSH‐UPDATE);

• HSELINE (OSH‐UPDATE);

• CISDOC (OSH‐UPDATE);

• CINAHL (EBSCO);

• Science Citation Index Expanded (including Conference Proceedings);

• NHS Economic Evaluation Database (NHS EED);

• European Network of Health Economic Evaluation Databases (EURONHEED);

• Cost‐Effectiveness Analysis Registry (CEA) at Tufts University.

We will also conduct a search for unpublished trials in ClinicalTrials.gov (www.clinicaltrials.gov) and the World Health Organization (WHO) 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 material.

Selection of studies

We will conduct the selection of eligible studies in two stages. First, two review authors (KG and LB) will independently screen titles and abstracts of all potentially relevant studies found with our systematic search to exclude studies that clearly do not fulfil the criteria for inclusion. The same review authors will code them as 'include' (eligible or potentially eligible/unclear) or 'exclude'. At this stage, we will exclude all references that clearly do not fulfil our inclusion criteria or that fulfil our exclusion criteria. Second, we will retrieve the full‐text study reports/publications and two review authors (KG and LB) will independently assess the full‐text and identify studies for inclusion. At this stage, we will include all references that fulfil our inclusion criteria. We will record reasons for exclusion of the ineligible studies assessed as full‐texts and report these in a 'Characteristics of excluded studies' table. We will resolve any disagreements through discussion. 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 study flow diagram.

Data extraction and management

We will use an Excel‐based data collection form for study characteristics and outcome data that has been piloted on at least one study in the review. Two review authors (KG and LB) will extract the following study characteristics from included studies.

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

• Participants: number of participants, number of clusters (hospitals or wards), mean age or age range, gender, inclusion criteria, and exclusion criteria.

• Interventions: description of intervention, comparison (elements included in safe handling in the control group), and cointerventions.

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

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

Two review authors (KG and LB) 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. One review author (KG) will transfer data into Review Manager 5 (RevMan 2014). We will double‐check that data are entered correctly by comparing the data presented in the systematic review with the study reports. A third review author (CT) will spot‐check study characteristics and data for accuracy against the trial report. Should we decide to include studies published in one or more languages in which our author team is not proficient, we will arrange for a native speaker or someone sufficiently qualified in each foreign language to fill in a data extraction form for us.

Assessment of risk of bias in included studies

For each RCT, two review authors (KG and LB) will independently assess risk of bias using criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreements by discussion. We will assess the risk of bias according to the following domains.

• Random sequence generation.

• Allocation concealment.

• Blinding of participants and personnel.

• Blinding of outcome assessment.

• Incomplete outcome data.

• Selective outcome reporting.

• Other bias (including source of funding and whether the duration of exposure to hazardous drugs in the intervention group and control group was measured reliably after ensuring that the participants were free from the outcome at the beginning of the study).

We will grade each potential risk 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 unblinded outcome assessment, risk of bias for a sample obtained and analysed by an automated machine may be very different than for an outcome such as time for preparation of the drug). 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.

For each non‐randomised study, the same two review authors (KG and LB) will assess the risk of bias independently using the risk of bias in non‐randomised studies of interventions (ROBINS‐I) tool (Sterne 2016). We will consider the following as possible sources of confounding.

• Changes or differences in layout, ventilation, fume cupboards, etc. that might lead to less contamination compared to the intervention.

• Changes or differences in policies that might lead to less contamination compared to the intervention.

• Education, training, and experience of healthcare staff that might lead to less contamination compared to the intervention.

• Differences in the supervision for drug preparation or drug administration that might lead to less contamination compared to the intervention.

• Changes or differences in other factors for genetic and chromosomal damage such as stress from work, working long hours, and smoking that might lead to fewer genetic and chromosomal abnormalities compared to the intervention.

• Differences in drug residue on a surface prior to contamination (e.g. thorough cleaning before the study in only group).

• Changes or differences in drug residue on the drug vials because of different batches or different manufacturers of the drug.

We will assess the risk of bias in the included economic evaluations using either the Consensus Health Economic Criteria (CHEC) list for assessment of methodological quality of economic evaluations (Evers 2005) or the Philips 2004 checklist.

We will consider all domains other than blinding of healthcare providers to be key domains. We will judge a study to have a high risk of bias overall 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 low risk of bias for all key domains.

When considering treatment 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 Review Manager 5 to calculate the treatment effects (RevMan 2014). We will use odds ratio if we include case‐control studies or risk ratio if we do not identify any case‐control studies for dichotomous outcomes (this is because risk ratios are much easier to interpret; however, risk ratios cannot be calculated in case‐controlled trials without the use of risk from another study), and mean differences for continuous outcomes. If only effect estimates and their 95% confidence intervals or standard errors are reported in studies, we will enter these data into Review Manager 5 using the generic inverse variance method (RevMan 2014). 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 interrupted time‐series studies, we will extract data from the original papers and reanalyse them according to the recommended methods for analysis of interrupted time‐series studies designs for inclusion in systematic reviews (Ramsay 2003). 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 intra‐cluster 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 obtain missing numerical outcome data where possible (e.g. 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 are missing, such as standard deviations or correlation coefficients, and they 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, outcome, and follow‐up. We will consider populations as similar when they are staff who are exposed to infusional hazardous drugs, for example, oncology nurses or pharmacists who handle infusional hazardous drugs. We will consider interventions as similar when it is clear that the system is a closed‐system drug transfer device. We will combine results data produced by each of the measures of contamination separately (e.g. urine tests, surface contamination, atmospheric contamination, and surface contamination) and we will combine cancer‐ and fertility‐related outcome data separately. We will regard follow‐up times of up to one year, between one to five years, and longer than five years as different.

We will use the I² statistic to measure heterogeneity among the trials in each analysis. If we identify substantial heterogeneity (above 50% as per Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011)), we will report it and explore possible causes by prespecified subgroup analysis.

Assessment of reporting biases

If we are able to pool more than five trials in any single meta‐analysis, we will create and examine a funnel plot to explore possible small‐study biases. We will use Egger's test to identify reporting biases (Egger 1997). We will consider a P value of less than 0.05 as statistically significant reporting bias.

Data synthesis

We will pool data from studies we judge to be clinically homogeneous using Review Manager 5 software (RevMan 2014). If two or more studies provide usable data in any single comparison, we will perform meta‐analysis. However, we will not pool data from different study designs (i.e. RCT and non‐randomised studies). For costs, we will use an international exchange rate based on purchasing power parities (PPPs) to convert cost estimates to UK pound sterling (GBP), and we will use the gross domestic product (GDP) deflators (or implicit price deflators for GDP) to convert cost estimates to 2017 GBP using PPP conversion rates and GDP deflator values available from the International Monetary Fund in the World Economic Outlook Database (updated biannually: see www.imf.org/external/data.htm). We will use both a fixed‐effect model and a random‐effects model to perform the meta‐analyses and will report the more conservative model. When the I² statistic is higher than 75%, we will not pool results of studies in meta‐analysis.

Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons (e.g. device A versus safe handling and device B versus safe handling) are combined in the same meta‐analysis, we will halve the control group to avoid double‐counting.

Subgroup analysis and investigation of heterogeneity

We will carry out the following subgroup analyses.

• Study design: CBA studies versus other non‐randomised study designs; unit of analysis is individual versus unit of analysis is cluster.

• Professional role: pharmacy technician versus chemotherapy nurse versus other healthcare staff.

• Duration of possible exposure.

• Intervention: any closed‐system drug‐transfer device.

• Control: safe handling following UK HSE standards.

We will perform subgroup analyses for primary outcomes (i.e. immediate to short‐term contamination, short‐term health benefits, long‐term reproductive health benefits, and development of any type of cancers). We will use the Chi² test to test for subgroup interactions in Review Manager 5 (RevMan 2014).

Sensitivity analysis

We will perform a sensitivity analysis defined a priori to assess the robustness of our conclusions. This will involve studies with low risk of bias versus studies with high risk of bias.