Types of studies

We will include any study that compares outcomes in the intervention group to outcomes in a control group that did not get the intervention. We will include randomised control trials and non‐randomised studies of interventions (NRSI); that is, prospective experimental studies with a concurrent control where the allocation of participants to intervention and control groups was not random (e.g. participants chose by themselves).

We will not include observational studies, such as natural experiments, in which the researchers did not introduce the intervention. This is because it is difficult to predict if the effects can be translated to real experiments in which the intervention is introduced by stakeholders. We will not include cross‐sectional studies because disease incidence can fluctuate rapidly and the temporal association is impossible to determine. We will not include mathematical modelling studies due to their limitations resulting from their many assumptions. We also assume that there is empirical evidence available, being more than one year into the pandemic.

We will include studies reported as full‐text articles, those published as abstract only, and unpublished data. We will also include preprints. We will not impose any language or date restrictions. 

Types of participants

We will include adults (> 18 years), both those who come into close contact with clients or customers (e.g. public‐facing employees such as cashiers or taxi drivers), and those who do not, but who can be infected by co‐workers. We will exclude studies involving healthcare workers (including dentists and other allied health professionals), as they are considered in separate Cochrane Reviews. We will include studies on workers at social care and home care services if they are not caring for people with SARS‐CoV‐2. We will exclude studies in children in primary and secondary school and students at universities. We will include studies in paid workers (i.e. employed workers) and exclude studies exclusively in people working on a volunteer basis.

We will include studies on severe acute respiratory syndrome (SARS) and Middle East respiratory syndrome (MERS). We will then differentiate between direct evidence from SARS‐CoV‐2 studies and indirect evidence from SARS and MERS studies in subgroup analyses (Subgroup analysis and investigation of heterogeneity).

We will include any study if at least 80% of the participants meet the review criteria as defined above, or if there are data for the relevant subset of participants in whom we are interested. We will explore differences in subgroup analyses. 

Types of interventions

We will include interventions that attempt to prevent or reduce workers' exposure to SARS‐CoV‐2 in the workplace. We will define categories of intervention according to the hierarchy of hazard controls. Consequently, the interventions to be included in our review are as follows.

Elimination (i.e. eliminating the source of SARS‐CoV‐2)

• Polymerase chain reaction (PCR) or rapid antigen testing with self‐isolation policy and quarantining close‐contact co‐workers

• Education regarding COVID‐19 symptoms and sickness absence policy for symptomatic individuals

• Automated processes (e.g. production lines)

Engineering controls

• Walk‐through disinfection systems

• Air‐purification systems (including, but not limited to, misting/fogging machines or high‐efficiency particulate absorbing (HEPA) filters)

• Installation of or improvement to ventilation (including installation of new systems)

• Barriers to separate or distance co‐workers and workers from members of the public (e.g. Perspex, glass, metal shield)

• Use of ultraviolet (UV) lighting

• Reconfiguration of workplace to minimise contact with the public (e.g. safe collection points for customers)

• Closing work areas to prevent groups of people assembling (including cafeterias)

Administrative controls

• Personal protective equipment (PPE)

• Vaccination of workers (where this exists specific to a workforce or workplace)

• Distancing between colleagues in the workplace (so‐called social distancing), including details of distance used (e.g. 1 m, 2 m, etc.)

• Hand‐washing protocols (including use of hand sanitisers)

• Working from home (WFH, where it is possible to do so). Also, allowing flexible working hours to facilitate home‐schooling and other caring responsibilities.

• Checking temperature (i.e. thermal screening) on entering the workplace (could also include formal screening for symptoms)

• Workplace cleaning and disinfecting regimes (i.e. infection prevention and control (IPC) policies and standard operating procedures)

• Use of online, rather than face‐to‐face, meetings (i.e. remote working arrangements)

• Cancelling or curtailing of work‐based travel

• Variation in start times, finish times, lunch and other work breaks to minimise contact with work colleagues (i.e. staggered rosters)

• Forming 'isolation bubbles' within the workplace to avoid mixing between different work teams (i.e. staffing bubbles)

• Facilitating travel to work in private cars, rather than having to use public transport (e.g. paying for parking)

• Cancelling work‐related out‐of‐hour social activities

• Introducing one‐way walk systems in workplaces

• Paid sick days

We will include interventions not listed here that also aim to reduce exposure to SARS‐CoV‐2 in the workplace. 

We will include combinations of eligible interventions.

Eligible interventions may be compared to:

• standard IPC practices in the workplace prior to the COVID‐19 pandemic (e.g. what deviation, if any, from pre‐existing IPC standard operating procedures were initiated since the COVID‐19 epidemic);

• no intervention to reduce exposure to SARS‐CoV‐2;

• a different intervention to reduce exposure to SARS‐CoV‐2; or

• different combinations of interventions to reduce exposure to SARS‐CoV‐2.

Types of outcome measures

Primary and secondary outcomes are listed below. Where applicable, we have specified relevant time frames and how the outcomes may be measured. However, we acknowledge that exact details are difficult to determine in a rapidly changing situation, and additional measures may appear important. We will consider the following follow‐up times for outcome measurement: short term, defined as less than 3 months after the intervention started; medium term, defined as between 3 and 12 months; and long term, defined as 12 months or longer. In situations where multiple time points are reported, we will include the longest follow‐up time from each study for analysis. All follow‐up time data will be reported descriptively.

We are considering SARS‐CoV‐2 infections and other respiratory diseases (SARS, MERS) as a surrogate for exposure to SARS‐CoV‐2, (SARS‐CoV‐1, MERS‐CoV). Development of a core outcome set (COS) for COVID‐19 prevention interventions, the COS COVID‐P study, is underway (COMET 2021). Work so far recommends that COVID‐19 infection is an essential outcome to measure in prevention studies, but has found that a number of different definitions are used (COMET 2021).

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 Ovid MEDLINE (see Appendix 1) for use in the other electronic databases. We used the following search strategies to develop our search.

• COVID‐19 terms for the MEDLINE strategy were modified from the CADTH Respiratory Pandemics (including COVID‐19, SARS, and MERS) ‐ MEDLINE filter (covid.cadth.ca/literature-searching-tools/cadth-covid-19-search-strings/#covid-19-medline).

• The study design filter was modified from the CADTH Randomised Controlled Trials / Controlled Clinical Trials – OVID Medline, Embase and PsycINFO filter (www.cadth.ca/resources/finding-evidence/strings-attached-cadths-database-search-filters#rand).

• The text words for occupational categories in the workplace were informed by the Centers for Disease Control and Prevention Interim List of Categories of Essential Workers (www.cdc.gov/vaccines/covid-19/categories-essential-workers.html).

We will impose no restriction on language of publication. We will arrange for the translation of key sections of potentially eligible non‐English language papers, or we will arrange for people who are proficient in the publications' languages to fully assess them for potential inclusion in the review as necessary.

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

• Cochrane Central Register of Controlled Trials (CENTRAL) (Cochrane Library).

• MEDLINE (Ovid) (Appendix 1).

• Embase (Ovid) (embase.com).

• NIOSHTIC‐2 (OSH‐UPDATE) (National Institute for Occupational Safety and Health bibliographic database).

• HSELINE (OSH‐UPDATE) (Health and Safety Executive Library and Information Service).

• CISDOC (OSH‐UPDATE) (International Labor Organization occupational safety and health bibliographic database).

• CISILO (International Occupational Safety and Health Information Centre bibliographic database).

• Web of Science Core Collections.

• Cochrane COVID‐19 Study Register (covid-19.cochrane.org/); via the Cochrane Register of Studies (crsweb.cochrane.org/).

• World Health Organization (WHO) COVID‐19 Global literature on coronavirus disease (search.bvsalud.org/global-literature-on-novel-coronavirus-2019-ncov/).

We will also conduct a search of unpublished and ongoing trials in ClinicalTrials.gov (www.clinicaltrials.gov/), the WHO International Clinical Trials Registry Platform (www.who.int/clinical-trials-registry-platform), and medRxiv (www.medrxiv.org/). 

If studies are published in languages other than those our review team can accommodate (Danish, Dutch, English, French, German, Italian, Portuguese, Spanish, and Swedish), we will consider involving Cochrane TaskExchange to identify people within Cochrane to translate these studies.

Searching other resources

We will check the 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

We will screen titles and abstracts using Covidence (Covidence). Review authors (ABP, KN, SR, KS, EP, BNS, JEV, OS, SD, DM, TF, MVT, CG, MB) will screen titles and abstracts independently and in duplicate, and exclude studies that clearly do not fulfil the criteria for inclusion.

We will retrieve the full texts of potentially eligible records and a pair of review authors (ABP, KN, SR, KS, EP, BNS, JEV, OS, DM, MVT, MB) will assess these to identify studies for inclusion. We will resolve any disagreements through discussion or, if required, through consulting a third review author (SD or CM).

We will record reasons for exclusion of studies assessed at the full‐text screening stage and report this in a PRISMA flow chart and in the 'Characteristics of excluded studies' table.

We will identify and exclude duplicates, and collate multiple reports of the same study so that each study is the unit of interest.

Should our systematic searches identify studies conducted by authors of this review, we will make sure to avoid conflict of interest by having all decisions concerning inclusion and exclusion, data extraction, and risk of bias assessment, made by review authors who were not involved with the study.

Because of the breadth of the review, review authors will communicate regularly whilst conducting screening to monitor the process and to avoid leaving numerous discrepancies to resolve at the end of the process.

Studies will be included regardless of language of publication.

We will document the details of the search strategy used and the number of records retrieved from each database (total number retrieved) or Internet search performed (total number screened) in accordance with PRISMA guidance (Page 2021).

Data extraction and management

We will use a data collection form for study characteristics and outcome data which has been piloted on 20 studies representing different intervention types. Review authors (ABP, KN, EP, BNS, SD, JEV, SR, KS) will extract the following study characteristics from included studies independently and in duplicate.

• Publication details: author, study source (e.g. journal publication, preprint, peer‐reviewed).

• Methods: study design, total duration of study, study location (e.g. country, city), study setting (e.g. type of workplace), withdrawals/missing data and how they were handled.

• Participants: number included/randomised, mean age or age range, sex/gender, severity of condition, diagnostic criteria if applicable, inclusion criteria, and exclusion criteria.

• Interventions: description of intervention (category and type), comparison, duration (including date of implementation), intensity, and co‐interventions.

• Outcomes: description of primary and secondary outcomes and measures specified and collected, and time points for reporting.

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

We will note in the 'Characteristics of included studies' tables if outcome data were not reported in a usable way. We will resolve disagreements by consensus or by involving a third review author (SD, MB, or CM). One review author (ABP) will transfer data into RevMan Web (RevMan Web 2020). A second review author (EP) will check study characteristics for accuracy against the primary study.

Assessment of risk of bias in included studies

Review authors (ABP, SR, KS, EP, BNS, JEV,, SD) will independently and in duplicate assess the risk of bias for each study, using the Cochrane risk of bias 2 tool (RoB2) (Sterne 2019), and the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions for each study design (Higgins 2021, hereafter referred to as the Cochrane Handbook). We will resolve any disagreements through discussion or by involving another author (MB or CM).

As we anticipate a wide array of included study designs, we have elaborated on multiple, potentially applicable tools below, in accordance with a recent comparable Cochrane Review on SARS‐CoV‐2 (Burns 2021).

For randomised controlled trials (RCTs), we will use the Cochrane RoB 2 tool, which assesses the risk of bias according to these domains:

• bias arising from the randomisation process (random sequence generation, allocation concealment, blinding of participants and personnel);

• bias due to deviations from intended interventions; we are interested in the 'intention‐to‐treat effect';

• bias due to missing outcome data;

• bias in measurement of the outcome; and

• bias in selection of the reported result.

We will use the appropriate RoB2 Excel tool to assess cluster‐RCTs and cross‐over trials.

We will grade each potential risk of bias as high, low, or some concerns, and provide a quote from the study report, together with a justification for our judgment, in the risk of bias tables. We will add additional domains for other study designs to the risk of bias tables. 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 all‐cause mortality may be very different from a quality of life assessment). Where information on the risk of bias relates to unpublished data or correspondence with a trial author, we will note this in the risk of bias table.

For assessing the risk of bias in NRSIs, we will use the Risk of Bias in Non‐Randomised Studies of Interventions (ROBINS‐I) tool (Sterne 2016). Our target trial against which we will assess the risk of bias would be a trial in which adults are assigned to a group with interventions in place that aim to reduce COVID‐19 infection at the workplace or standard practice or alternative interventions. We will consider the following variables as potential confounders: age, sex, ethnicity, comorbidities, and socioeconomic status. We will first use the signalling questions as prescribed in the ROBINS‐I tool and then assess the risk of bias if these questions indicate a potential risk of bias.

We will assess these risk of bias domains:

• bias due to confounding;

• bias due to selection of participants into the study;

• bias in the classification of interventions;

• bias due to deviation of intended interventions;

• bias due to missing data;

• bias due to outcome measurement;

• bias in selection of the reported result.

We will judge the risk of bias of NRSIs in all the above domains to be low, moderate, serious, or critical.

We will assess the risk of bias for these key outcomes, which will be included in the summary of findings tables:

• incidence rate of SARS‐CoV‐2 (or other viruses) infection;

• SARS‐CoV‐2‐related mortality;

• adverse events, including but not limited to cutaneous and respiratory events, accidents, depression, anxiety;

• all‐cause mortality;

• quality of life as defined by authors;

• hospitalisation;

• adherence to strategies (e.g. use of hand sanitiser, wearing of face masks, degree of social distancing), measured using an ordinal scale (e.g. Likert).

Measures of treatment effect

We will enter the outcome data for each study into the data tables in RevMan Web to calculate the treatment effects (RevMan Web 2020). Where possible, we will convert these effect estimates to a common format to allow meta‐analysis. We will use odds ratios for binary outcomes, and mean differences or standardised mean differences for continuous outcomes, or other types of data as reported by the authors of the studies. Where binary measures of effect estimates have been reported using an alternative format to an odds ratio, we will convert alternative effect estimates (risk ratios, risk differences, rate ratio) into odds ratios using available information (e.g. baseline or control group risk).

If only effect estimates and their 95% confidence intervals or standard errors are reported in studies, we will enter these data into RevMan Web using the generic inverse variance method (RevMan Web 2020). 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, we will describe them in the 'Characteristics of included studies' table, or enter the data into Additional tables.

For interrupted time series (ITS) studies, we will extract data from the original papers and re‐analyse them according to the recommended methods for the analysis of ITS designs for inclusion in systematic reviews (Ramsay 2003). We will use the standardised change in level and change in slope as effect measures. For other non‐randomised studies, we will extract the estimate of intervention effect together with a measure of precision (confidence interval or standard error) and information about the method of analysis and adjustment for confounders. If both unadjusted and adjusted intervention effects are reported, then adjusted effects will be chosen in preference. Some non‐randomised studies report multiple adjusted estimates from analyses, including different sets of covariates. If multiple adjusted estimates of intervention effect are reported, we will choose the one that is judged to minimise the risk of bias due to confounding, after discussion between review authors (see Chapter 25, Section 25.2.1). We will present randomised and non‐randomised studies as separate subgroups, without aggregation.

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 clustering, we will inflate the standard errors using the design effect. We will calculate the design effect based on a fairly large assumed intra‐cluster correlation co‐efficient. We base this assumption of 0.10 being a realistic estimate by analogy with studies about implementation research (Campbell 2001). We will explore this assumption using sensitivity analysis, as clustering may be high in the context of COVID‐19. We will follow the methods described in the Cochrane Handbook for the calculations (Higgins 2021). Note that cluster‐randomisation could be at the level of the workplace (e.g. a factory), a subset of the workplace (e.g. department or shift) or a larger unit (e.g. a geographical area), and we will take care to ensure that the analysis makes appropriate adjustment for clustering at the correct level.   

When cross‐over trials report continuous outcomes with which the authors have not reported a paired analysis, we will perform a paired analysis based on a reported or imputed correlation between the outcomes of the intervention and the control condition, as advised in Chapter 16 of the Cochrane Handbook (Higgins 2021). For dichotomous outcomes, we will adjust the confidence intervals for the paired analysis according to Elbourne 2002.

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 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 intra‐cluster 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 (Higgins 2021).

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 any workplace populations as similar enough to combine.

• We will consider interventions as similar when they are from the same sub‐category within the hierarchy of controls (as listed in Types of interventions).

• We will consider any outcome measure relating to the rate of SARS‐CoV‐2 as similar enough to combine. We will not combine data on SARS‐CoV2 with data on SARS or MERS.

• We have categorised follow‐up times as follows: short term as less than 3 months after the intervention has begun; medium term as between 3 and 12 months; and long term as 12 months or longer. We will consider short‐ and long‐term follow‐up times as different, whereas we will combine short‐ and medium‐term outcomes or medium‐ and long‐term outcomes where relevant.

Despite the aforementioned points, we recognise that we cannot anticipate all of the various populations, interventions, outcomes, and follow‐up times that the included studies will report on and their potential comparability and compatibility. As such, we will perform our full assessment of heterogeneity and definition of follow‐up times after evaluating the included studies. We will reach decisions after consulting the entire author team to consider both Cochrane and occupational medicine viewpoints.

As well as visual inspection of forest plots, we will use the I² statistic to assess heterogeneity amongst the trials in each analysis. If we identify substantial heterogeneity, we will report it and explore possible causes by prespecified subgroup analysis. We will consider heterogeneity as substantial if I² is above 50%.

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 we judge to be clinically homogeneous, as defined in the section Assessment of heterogeneity, using RevMan Web (RevMan Web 2020). If more than one study provides usable data in any single comparison, we will perform meta‐analysis. We will use a random‐effects model because we believe that the type of intervention and study designs included will always lead to heterogeneity. 

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

Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons (e.g. intervention A versus no intervention, and intervention B versus no intervention) are combined in the same meta‐analysis, we will halve the no intervention group to avoid double‐counting.

We will refer to SWiM guidelines for synthesis without meta‐analysis if this is the case in this review (Campbell 2020).

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses.

• Dose (intensity, duration of the intervention).

• Sector (e.g. transportation, agriculture, tourism, manufacturing, construction, forestry and fishing, mining and quarrying, electricity, gas, steam and air conditioning supply, water supply; sewerage, waste management and remediation activities, wholesale and retail trade; repair of motor vehicles and motorcycles, transportation and storage, accommodation and food service activities, information and communication, financial and insurance activities, real estate activities, professional, scientific and technical activities, administrative and support service activities, public administration and defence; compulsory social security, education, human health and social work activities, arts, entertainment and recreation, other service activities, activities of households as employers; undifferentiated goods‐ and services‐producing activities of households for own use, activities of extraterritorial organisations and bodies) (UNIDO 2015).

• Geographic region (Africa, Asia, Caribbean, Central America, Europe, North America, Oceania, and South America).

• Country income‐level (high, upper‐middle, lower‐middle, low‐income).

• The time frame of the pandemic during which the study was conducted (early and late based upon the median).

• Studies in which both intervention and control groups use PPEs.

• Studies that include only a subset of relevant participants,

• SARS‐CoV‐2 studies versus indirect evidence from SARS and MERS studies.

• Funding (public/governmental vs industry/commercial).

• Public‐facing versus non‐public‐facing workplaces.

We will use the three primary outcomes in subgroup analyses. We will use the Chi² test to test for subgroup interactions in RevMan Web (RevMan Web 2020).

Sensitivity analysis

We will perform 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;

• excluding studies with estimated presumably intra‐cluster correlation co‐efficient  (ICC) (or using alternative ICCs);

• non‐peer‐reviewed publications (preprints, abstracts only) versus peer‐reviewed publications.

We will also perform sensitivity analyses to check how our assumptions influence the conclusions of the review.

Summary of findings and assessment of the certainty of the evidence

We will create summary of findings tables for all comparisons of workplace interventions with no intervention or standard practices.

For these comparisons, we will report the following outcomes.

• Incidence rate of SARS‐CoV‐2 (or other viruses) infection.

• SARS‐CoV‐2‐related mortality.

• Adverse events, including but not limited to cutaneous and respiratory events, accidents, depression, anxiety.

• All‐cause mortality.

• Quality of life as defined by authors.

• Hospitalisation.

• Adherence to strategies (e.g. use of hand sanitiser, wearing of face masks, degree of social distancing), measured using an ordinal scale (e.g. Likert).

We will use 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 contribute data to the meta‐analyses for the prespecified outcomes. We will use methods and recommendations described in the Cochrane Handbook (Higgins 2021), using GRADEpro software (GRADEpro GDT)  We will justify all decisions to down‐ or upgrade the quality of studies using footnotes.

We will prioritise the evidence from RCTs. Because of the inclusion of non‐randomised studies, if necessary, we will compile an additional summary of findings table showing all our GRADE decisions about the quality of evidence and their justifications. If we include RCTs and non‐RCTs for the same outcome, we will base our GRADE assessments on the evidence from RCTs. If only a non‐RCT reports a key outcome, we will assess it using GRADE.