Types of studies

We considered all published and unpublished randomized controlled trials (RCTs) and controlled before and after studies (CBAs) as eligible for inclusion in this review. 

Types of participants

We included healthcare workers who interact with patients, patient advocates, or both, in any public or private healthcare facility regardless of worker age, gender, or profession. These included:

• physicians and physician assistants;

• dentists;

• nurses and midwives;

• allied health professionals (e.g. physiotherapists, occupational therapists, speech pathologists, pharmacists, respiratory therapists, medical imaging technicians, oral hygienists, podiatrists, dieticians, opticians); and

• healthcare support personnel (e.g. reception staff, healthcare aides or assistants, healthcare security personnel).

Types of interventions

We included any educational or training intervention undertaken with healthcare workers to improve their knowledge, attitudes, and skills in preventing and minimizing verbal or physical aggression directed toward them and their workplace peers from patients or their advocates. These included interventions designed to enhance knowledge and understanding of legal responsibilities, organizational policies and procedures, and specific risk assessment and control strategies. Interventions included education and training in specific communication and behavior management techniques targeting the diffusion and de‐escalation of aggression, violence avoidance and breakaway strategies, and physical restraint of aggressive people.

We included interventions that were mandatory or voluntary; delivered all at once or over multiple sessions; and delivered face‐to‐face, online, or in blended form and including synchronous or asynchronous components. We included interventions delivered in workplace, educational, and other professional settings. We included stand‐alone programs as well as those offered in conjunction with other organizational interventions, but only when such interventions were "controlled for" in the analysis of impact or outcomes, or when they could be determined not to have confounded or biased results of the education and training intervention study. 

Types of outcome measures

Outcome measures included reported clinical events and participant‐reported outcomes.

Electronic searches

We searched the following electronic databases from their inception to the date of the search specified to identify potential studies. 

• Cochrane Central Register of Controlled Trials (CENTRAL), in the Cochrane Library (June 2020).

• MEDLINE (PubMed, June 2020).

• Embase (June 2020).

• Cumulative Index to Nursing and Allied Health Literature (CINAHL) (EBSCO, June 2020).

• PsycINFO (ProQuest, June 2020).

• US National Institute for Occupational Safety and Health bibliographic database of literature on occupational safety and health (NIOSHTIC) (OSH‐UPDATE, June 2020).

• NIOSHTIC‐2 (OSH‐UPDATE, June 2020).

• HSELINE (OSH‐UPDATE, June 2020).

• ISDOC (OSH‐UPDATE, June 2020).

We used keywords selected from the search strategies supplied in Appendix 1.

Searching other resources

We also conducted a search of the following. 

• ClinicalTrials.gov (www.ClinicalTrials.gov) and the World Health Organization (WHO) trials portal (www.who.int/ictrp/en/).

• WorkSafe Australia.

• Canadian Centre for Occupational Health and Safety (CCOHS).

• The Campbell Collaboration and social, psychological, educational, and criminological trials register.

We checked the reference lists of all primary studies and review articles for additional references. Finally, we contacted experts in the field to identify additional unpublished materials. 

Selection of studies

Four review authors (JP, AH, SR, SGe) independently screened titles and abstracts of all potentially eligible studies identified as a result of the search and coded them as "retrieve" (eligible or potentially eligible/unclear) or "do not retrieve." We retrieved the full‐text study reports/abstracts/publications, and five review authors (HR, TD, SG, BM‐J, SGe) independently screened the full text and identified studies for inclusion. When a study was identified as ineligible for inclusion in the review, we recorded the reason(s) for its exclusion. We resolved disagreements by consensus or by consultation with another person from the review team (DH, SGe). We identified and excluded duplicates and collated multiple reports of the same study, so that each study, rather than each report, is the unit of interest in the review. We recorded this selection process in sufficient detail to complete a PRISMA flow diagram and Characteristics of excluded studies table.

Data extraction and management

We used a study‐specific data collection form for collection of study characteristics, intervention details, and outcome data (Appendix 2). All review authors piloted this form on one study in the review. Four review authors (HR, AH, SG, SGe) extracted study characteristics from the identified included studies. 

Using the study‐specific data collection form, we extracted the following study characteristics.

• Publication details: authors, email address of corresponding author, date of publication, title, journal name, volume, issue, pages.

• Methods: study design (e.g. RCT/cluster RCT/CBA), including sampling, group allocation and treatment of missing data, study location/s, study setting/s, withdrawals.

• Participants: health worker type/s, total number of participants, number of health worker type sub‐populations and proportions (%), mean age or age range, gender, workplace/s (e.g. mental health, emergency department), work setting/s (e.g. hospital inpatient, hospital outpatient, community), work sector/s (e.g. public, private, non‐government), inclusion and exclusion criteria.

• Interventions: description of interventions and co‐interventions, targeted knowledge, attitudes and skills, comparison, content of both intervention and control condition, and co‐interventions (especially noting if bundled with other organizational interventions), duration, intensity, number commencing, number completing, adherence to protocol.

• Outcomes: description of primary and secondary outcomes specified and collected, measurement instruments used and validation status (e.g. reported/not reported), at which time points reported, controlling for biasing or confounding effects of co‐interventions.

• Length of follow‐up: time points at which primary and secondary outcomes were collected; categorization to short‐term, medium‐term, and long‐term follow‐up (see further details below in Assessment of heterogeneity).

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

Upon preparation of the final included list of studies, three review authors (DH, SR, SGe) independently extracted data from these study reports. We noted in the Characteristics of included studies table if outcome data were not reported in a usable way. One review author (TD) transferred data into Review Manager 5 (RevMan 5.3.) Another (SGe) made the migration toward Review Manager Web (RevMan Web 2019). We double‐checked that data were entered correctly by comparing data presented in the systematic review with information provided in the study reports. Two review authors (JP, SGe) spot‐checked study characteristics for accuracy against the study report.

Assessment of risk of bias in included studies

Four authors of the present review (DH, TD, BM‐J, SGe) independently assessed risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Disagreements were resolved by discussion or by consultation with another review author (AH, HR, JP, SG, or SR). Risk of bias of the included RCTs was assessed 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 biases.

Each potential source of bias was graded as high, low, or unclear. Further, a quote from the study report was provided together with a justification for the assessment in the "Risk of bias" table. The risk of bias judgment is summarized across different studies for each of the domains listed. Blinding was considered separately for different key outcomes when necessary (e.g. for unblinded outcome assessment, risk of bias for all‐cause mortality may be very different than for a participant‐reported pain scale). However, blinding was not found to be necessary for evaluation of risk of bias of the included studies. When information on risk of bias was related to unpublished data or correspondence with a trialist, this was noted in the "Risk of bias" table.

For CBAs, we used a combination of the applicable domains for risk of bias determination for RCTs and elements of the Downs and Black checklist (Downs 1998), as described in Chapter 13 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

Measures of treatment effect

Outcome data for each study were entered into the data tables in Review Manager Web to calculate treatment effects (RevMan Web 2019). We used risk ratios (RRs) for dichotomous outcomes and standardized mean differences (SMDs) for continuous outcomes, or other types of data as reported by study authors. When only effect estimates and their 95% confidence intervals (CIs) or standard errors were reported in studies, we entered these data into Review Manager Web using the generic inverse‐variance method. We ensured that higher scores for continuous outcomes have the same meaning for the particular outcome, explained the direction to the reader, and reported when the directions were reversed, if this was necessary. When results could not be entered either way, we described them in the Characteristics of included studies table, or we entered the data into Additional tables. 

Unit of analysis issues

For studies that employed a cluster‐randomized controlled trial (CRCT) design and that reported sufficient data for inclusion in the meta‐analysis but did not make an allowance for the design effect, we calculated the design effect based on a fairly large assumed intracluster correlation of 0.10 (Appendix 3). We based this assumption of 0.10 as a realistic estimate by analogy to studies about implementation research (Campbell 2001). We followed the methods stated in the Cochrane Handbook for Systematic Reviews of Interventions to perform the calculations (Higgins 2011).

Dealing with missing data

We contacted investigators or study sponsors to verify key study characteristics and obtain missing numerical outcome data when possible (e.g. when a study is identified as an abstract only). When this was not possible and the missing data were thought to introduce serious bias, we explored the impact of including such studies in the overall assessment of results by conducting a sensitivity analysis. 

If numerical outcome data such as standard deviations or correlation coefficients were missing and we could not obtain these from trial authors, we calculated 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 assessed the homogeneity of the results of all included studies based on similarity of study design, intervention types, outcomes, and follow‐up. We considered interventions to be different when they included education only or education combined with training. RCTs and CBAs were considered separately.

We categorized studies based on mode of delivery (online or face‐to‐face) and on their duration (short for less than a week, long for one week or longer, and self‐paced). We did not assume that these differences could cause differences in the effect estimates. Still, we did run subgroup analysis to check for any differences in both mode of delivery and length of interventions. We reported the results of this analysis both combined and separated when subgroup differences were found.

Further, follow‐up times were categorized into short‐term (six months and less), medium‐term (between six months and 12 months), and long‐term (12 months and longer) follow‐up and were regarded as different.

Statistical heterogeneity was assessed using the I² statistic (Higgins 2011), based on the following as a rough guide for interpretation: 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. In cases of substantial heterogeneity (defined as I² ≥ 50%), we explored the data further, including subgroup analyses, in an attempt to explain the heterogeneity.

Assessment of reporting biases

Because we were not able to pool 10 or more trials in any single meta‐analysis, we did not explore possible small‐study biases via funnel plot examination. 

Data synthesis

We pooled the data from studies judged to be homogeneous using Review Manager Web software (RevMan Web 2019). If more than one study provided usable data for any single comparison, we performed meta‐analysis. When studies were statistically heterogeneous, we used a random‐effects model. Otherwise, we used a fixed‐effect model. When using the random‐effects model, we conducted a sensitivity check by using the fixed‐effect model to reveal differences in results. We included a 95% confidence interval for all estimates. 

When multiple trial arms were reported in a single trial, we included only the relevant arms. If two comparisons were combined in the same meta‐analysis, we halved the control group to avoid double‐counting.

Subgroup analysis and investigation of heterogeneity

The original protocol intended to carry out subgroup analyses if a sufficient number of studies were found based on types of delivery and length of intervention. As such, we carried out subgroup analyses when a sufficient number of studies with substantial heterogeneity (I² > 50%) were found among the included studies based on:

• types of delivery (face‐to‐face or online); and

• duration of intervention (short, long, or self‐paced). 

Sensitivity analysis

We originally planned to carry out sensitivity analysis to test the robustness of our meta‐analysis results by omitting studies that we judged to be at high risk of bias. However, we did not find a sufficient number of studies to perform sensitivity analyses. 

Summary of findings and assessment of the certainty of the evidence

A "Summary of findings" table was created for each of the following outcomes.

• Episodes of aggression.

• Changes in personal knowledge, attitudes, and skills related to workplace aggression.

• Adverse personal and organizational outcomes attributable to incidents of workplace aggression.

We evaluated the quality of available evidence using the GRADE approach. We generated a "Summary of findings" table that provides outcome‐specific information concerning the overall quality of evidence from studies included in the comparison, the magnitude of effect of the interventions examined, and the sum of available data on outcomes considered. We included information on the primary and secondary outcomes of our review. We assessed the quality of evidence using several factors.

• Limitations in study design and implementation of available studies.

• Indirectness of evidence.

• Unexplained heterogeneity or inconsistency of results.

• Imprecision of effect estimates.

• Potential publication bias.

For each outcome, we classified the quality of evidence according to the following categories.

• High quality: further research is very unlikely to change our confidence in the estimate of effect.

• Moderate quality: further research is likely to have an important impact on our confidence in the estimate of effect, and may change the estimate.

• Low quality: further research is very likely to have an important impact on our confidence in the estimate of effect, and is likely to change the estimate.

• Very low quality: we are very uncertain about the estimate.

We used the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness, and publication bias) to assess the quality of a body of evidence as it relates to the studies that contributed data to meta‐analyses for the pre‐specified outcomes. We adhered to the methods and recommendations described in Section 8.5 and Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions, using GRADEpro software (GRADEPro 2014; Higgins 2011). We justified all decisions to downgrade the quality of RCTs or to upgrade the quality of CBAs using footnotes, and we made comments to aid the reader's understanding of the review when necessary. Criteria for upgrading included a large effect size, a reported dose‐response gradient, and the effects of all plausible confounding factors working against the intervention.