Criteria for considering studies for this review
Types of studies
We included all randomised controlled trials (RCT), cluster-randomised trials (c-RCT), interrupted time-series (ITS) and controlled before and after studies (CBA) irrespective of language of publication, publication status, or blinding.
We expected that the availability of RCTs would be limited for this topic. Interventions for prevention are often very different from clinical interventions. Many interventions are not implemented at the individual level. For example, new equipment is used by a group of workers or safety engineering controls are applied to the whole department simultaneously. This approach makes individual randomisation impossible. In principle, this can be partly overcome by randomisation at the department level as in a c-RCT design. However, as the level of aggregation increases, the more difficult this is to perform due to the level of recruitment required. Therefore, we included the following non-randomised study designs in our review: CBA studies with a concurrent control group, and ITS. CBA studies are also called prospective cohort studies. They are easier to perform, taking into account that the intervention is assigned at the group level, and still have reasonable validity.
ITS designs are often based on routinely collected administrative data from insurance or governmental sources, collected for injury outcomes. In many cases the data are collected independently from interventions and over long periods of time, offering reasonable validity. If there are at least three data points before and three data points after the intervention, we included these study designs as ITS (EPOC 2006). Both ITS with and without a control group were eligible for inclusion.
Types of participants
We included studies where participants were HCWs, including dentists, which means all persons that are professionally involved in providing health care to patients. The majority of study participants had to fulfil this criterion.
Types of interventions
We included studies examining any medical devices that aim to prevent percutaneous exposure injuries and thus could reduce the risk of exposure to blood or bodily fluids.
We categorised the interventions based on the type of device in the following way.
- Safety engineered devices for blood collection.
- Safety engineered devices for Injecting fluids.
- Containers for collecting sharps.
Because these categories did not cover all studies that we found, we added two categories.
- The use of multiple safety devices in an intervention programme.
- Intravenous systems.
We excluded studies where sharp suture needles were substituted with blunted ones. Another Cochrane review (Parantainen 2011) has addressed the effect of this intervention. We also excluded studies on devices that eliminate the use of suture needles or that encapsulate suture needles during surgery because the risk of a needlestick injury is different with suture needles in surgery. Extra gloves or special types of gloves could theoretically be considered a device to prevent needlestick injuries while handling needles, but we excluded these studies because there is another Cochrane review in preparation on the effect of gloves to prevent needlestick injuries (Parantainen 2012).
Types of outcome measures
Our primary outcome measure was exposure of HCWs to potentially contaminated blood or bodily fluids. Exposure can be reported as self-reported needlestick injury, sharps injury, blood stains inside the gloves, or glove perforations. We considered all reports of such exposure as valid measures of the outcome, such as self-reports, reports by the employer, or observations of blood stains.
We considered ease of use of the devices (including user satisfaction) and information related to the cost of the intervention as secondary outcomes.
Search methods for identification of studies
First, we applied search terms for percutaneous exposure incidents. We then combined these terms for percutaneous exposure incidents with the recommended search strings for randomised trials and for non-randomised studies. We used the Robinson 2002 search strategy for randomised clinical trials and controlled clinical studies. For finding non-randomised studies, we used the sensitive search strategy for occupational health intervention studies (Verbeek 2005).
We used the strategy to search CENTRAL, MEDLINE, EMBASE, NHSEED, Science Citation Index Expanded, CINAHL, OSH-update, and PsycINFO from the earliest record to 27 January 2014. We also searched LILACS but only until 2012. We felt that the yield did not outweigh the efforts and decided to stop searching LILACS. In addition, we searched the databases of WHO, the UK National Health Service (NHS) and www.med.virginia.edu/epinet (Royle 2003).
We present the search strategies for the databases listed above in Appendix 1.
In an update of the basic search that is common with Parantainen 2011 and Parantainen 2012, we used recap* and device* as additional search terms combined by OR and with the other terms (Appendix 2).
Searching other resources
We screened the reference lists of all relevant studies for additional studies.
Data collection and analysis
Selection of studies
Using the inclusion and exclusion criteria, the authors (M-CL, JV, AP, MP) worked individually and independently to screen the titles and abstracts of the references that were identified by the search strategy as potential studies. Pairs of authors went through the same references to increase the reliability of the results. We obtained the full texts of those references that appeared to meet the inclusion criteria. We did not blind ourselves regarding the trial author details because we felt that it would not increase validity. We solved disagreements between pairs by discussion. A pair consulted a third author if disagreement persisted.
Data extraction and management
Review authors worked in pairs (AP and JV, M-CL and MP) but independently to extract the data onto a form. The form included the essential study characteristics about the participants, interventions, outcomes and results. We also noted any adverse events and the sponsorship of the study. Two pairs of authors (AP and JV, M-CL and MP) independently assessed the risk of bias of the studies. The pairs used a consensus method if disagreements occurred. The pairs consulted a third author if disagreement persisted. Again, we did not mask trial names because we believed that it would not increase validity.
Assessment of risk of bias in included studies
For the assessment of risk of bias in RCTs we used the risk of bias tool in RevMan 2011. For CBA studies, we used a validated instrument (Downs 1998). The instrument has been shown to have good reliability, internal consistency and validity. We used the score on internal validity to judge the risk of bias of the included studies. We scored all items as 1 when the criterion was fulfilled and 0 if this was unclear or not the case.
We used the score on the checklist to discern trials with a low risk of bias from trials with a high risk of bias. We labelled trials as having a high risk of bias when the score was less than 50% of the total attainable score. We reported the most pertinent items in the risk of bias tables in the 'Characteristics of included studies' table.
For ITS studies we used the risk of bias criteria as presented by Ramsay 2003.
Measures of treatment effect
For RCTs and CBA studies with dichotomous outcomes, we used relative risks or risk ratios (RR) as the measure of the treatment effect. We did not use odds ratios because the incidence of most outcomes was higher than 10% and then odds ratios give an inflated impression of the relative risk.
In studies where needlestick injuries or glove perforations were reported more than once for an individual we used rates and rate ratios as the treatment effect. We calculated the log rate ratio and the standard error and used these data as the input for RevMan.
For ITS studies, we extracted and re-analysed the data from the original papers according to the recommended methods for analysis of ITS designs for inclusion in systematic reviews (Ramsay 2003). These methods utilise a segmented time-series regression analysis to estimate the effect of an intervention while taking into account secular time trends and any autocorrelation between individual observations. For each study, we fitted a first order autoregressive time-series model to the data using a modification of the parameterization of Ramsay 2003. Details of the mode specification are as follows:
Y = ß0 + ß1 time + ß2 (time - p) I (time > p) + ß3 I (time > p) + E, E ˜ N (0, s2).
For time = 1,...,T, where p is the time of the start of the intervention, I (time ≥ p) is a function which takes the value 1 if time is p or later and zero otherwise, and where the errors E are assumed to follow a first order autoregressive process (AR1) and the errors E are normally distributed with mean zero and variance s2. The ß parameters have the following interpretation:
ß1 is the pre-intervention slope;
ß2 is the difference between post- and pre-intervention slopes;
ß3 is the change in level at the beginning of the intervention period, meaning that it is the difference between the observed level at the first intervention time point and that predicted by the pre-intervention time trend.
We used the change in slope and the change in level as two different measures of treatment effect for ITS studies.
Unit of analysis issues
For studies that employed a cluster-randomised design but did not make an allowance for the design effect, we intended to calculate the design effect. If no intra-cluster coefficients were reported, although they are needed to calculate the design effect, we would have assumed a fairly large intra-cluster coefficient of 0.05 to enable the calculation of design effect. We intended to use the methods that are recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) for the calculations. However, the two studies that used a cluster-randomised design either did not provide data on the size of the clusters (L'Ecuyer 1996 2wva) or had a loss to follow up of 50% (van der Molen 2011), which made the cluster calculations questionable. Therefore, we did not perform these calculations.
For studies with multiple study arms that belonged to the same comparison, we divided the number of events and participants in the control group equally over the study arms to prevent double counting of study participants in the meta-analysis (Asai 2002 active; Asai 2002 passive).
Dealing with missing data
We contacted the authors for additional information if the data needed for meta-analysis were missing (Hotaling 2009; Sossai 2010). If data were presented in figures only and the authors could not be reached, we extracted data from the figures presented in the article (Goldwater 1989). If data such as standard deviations had been missing and they could be calculated from other data present in the article, such as P values, we would have done so according to the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), but there were no studies where this was necessary.
Assessment of heterogeneity
Clinical homogeneity among studies was defined based on the similarity of populations, interventions, and outcomes measured at the same follow-up point. We regarded all healthcare professionals as sufficiently similar to assume a similar preventive effect from the use of similar devices. We categorised safe devices as indicated under types of interventions and assumed that different devices would lead to different effects. We added two extra categories: intravenous (IV) systems and the introduction of multiple safe devices at the same time.
We divided outcomes into a category of needlestick injuries and a category of blood or bodily fluid splashes. We deemed the devices contained within these categories to be conceptually similar and sufficiently homogeneous to be combined in a meta-analysis. Thus, we had two different outcome measures: needlestick injuries and blood splashes. Even though the denominator of the needlestick injury rates differed from patients to devices to workers we felt that they were sufficiently similar to be combined.
We did not combine various study designs as we assumed that there were large differences in risk of bias between the different study types. We have presented the results per comparison separately for each design type.
We assessed statistical heterogeneity by means of the I2 statistic. We used the values of < 40%, between 30% and 60%, between 50% and 90%, and over 75% as indicating not important, moderate, substantial, and considerable heterogeneity respectively, as proposed in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).
Assessment of reporting biases
We aimed to assess publication bias with a funnel plot if more than five studies were available in a single comparison.
We pooled studies that contained sufficient data and that we judged to be clinically and statistically homogeneous with RevMan 5 software (RevMan 2011).
When studies were statistically heterogeneous we used a random-effects model; otherwise we used a fixed-effect model.
For ITS, we first standardised the data by dividing the outcome and standard error by the pre-intervention standard deviation resulting in an effect size, as recommended by Ramsay 2001. Then, we entered the results into RevMan as the change in level and in slope as two different outcomes using the general inverse variance method.
Finally, we used the GRADE approach to assess the quality of the evidence per comparison and per outcome as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). For comparisons that only included RCTs, we started at high quality evidence. Then, we reduced the quality of the evidence by one or more levels if there were one or more limitations in the following domains: risk of bias, consistency, directness of the evidence, precision of the pooled estimate, and the possibility of publication bias. When the comparison included non-randomised studies we started off at the low quality level and downgraded further if there were limitations, or we would have upgraded the quality if there were reasons to do so. We intended to use the programme GRADEpro 2008 to generate summary of findings tables for the two most important comparisons and outcomes, but this was not possible because we found a range of study designs which could not be combined statistically. Instead, we presented the quality of evidence and our considerations per comparison in an additional table.
Subgroup analysis and investigation of heterogeneity
We intended to re-analyse the results for studies with a high baseline or control group exposure rate, and for studies from low- and middle-income countries, but this was not possible due to the few studies that we found and the lack of studies from low- and middle-income countries.
We intended to re-analyse the results including only studies with a low risk of bias in order to find out if risk of bias led to changes in the findings but there weren't enough studies to do so.