Joanne E McKenzie, Sue E Brennan, Rebecca E Ryan, Hilary J Thomson, Renea V Johnston, James Thomas

This chapter should be cited as: McKenzie JE, Brennan SE, Ryan RE, Thomson HJ, Johnston RV, Thomas J. Chapter 3: Defining the criteria for including studies and how they will be grouped for the synthesis. In: Higgins JPT, Thomas J, Chandler J, Cumpston M, Li T, Page MJ, Welch VA (editors). Cochrane Handbook for Systematic Reviews of Interventions. 2nd Edition. Chichester (UK): John Wiley & Sons, 2019:[insert chapter page numbers]

 

3.1 Introduction

One of the features that distinguishes a systematic review from a narrative review is that systematic review authors should pre-specify criteria for including and excluding studies in the review (eligibility criteria, see MECIR Box 3.2.a).

When developing the protocol, one of the first steps is to determine the elements of the review question (including the population, intervention(s), comparison(s) and outcomes, or PICO elements) and how the intervention, in the specified population, produces the expected outcomes (see Chapter 2, Section 2.4.1 and Chapter 17, Section 17.2.1). Eligibility criteria are based on the PICO elements of the review question plus a specification of the types of studies that have addressed these questions. The participants, interventions and comparisons in the review question usually translate directly into eligibility criteria for the review, though this is not always a straightforward process and requires a thoughtful approach, as this chapter shows. Outcomes usually are not part of the criteria for including studies, and a Cochrane Review would typically seek all sufficiently rigorous studies (most commonly randomized trials) of a particular comparison of interventions in a particular population of participants, irrespective of the outcomes measured or reported. It should be noted that some reviews do legitimately restrict eligibility to specific outcomes. For example, the same intervention may be studied in the same population for different purposes; or a review may specifically address the adverse effects of an intervention used for several conditions (see Chapter 14).

Eligibility criteria do not exist in isolation, but should be specified with the synthesis of the studies they describe in mind. This will involve making plans for how to group variants of the PICO elements for synthesis. This chapter describes the processes by which the structure of the synthesis can be mapped out at the beginning of the review, and the interplay between the review question, considerations for the analysis and their operationalization in terms of eligibility criteria. Decisions about which studies to include (and exclude), and how they will be combined in the review’s synthesis, should be documented and justified in the review protocol.

A distinction between three different stages in the review at which the PICO construct might be used is helpful for understanding the decisions that need to be made. In Chapter 2 (Section 2.3) we introduced the ideas of a review PICO (on which eligibility of studies is based), the PICO for the comparison (defining the question that each specific synthesis aims to answer) and the PICO of the included studies (what was actually investigated in the included studies). In this chapter, we focus on the review PICO and the PICO for the comparison as a basis for specifying which studies should be included in the review and planning its syntheses. These PICOs should relate clearly and directly to the questions or hypotheses that are posed when the review is formulated (see Chapter 2) and will involve specifying the population in question, and a set of comparisons between the intervention groups.

An integral part of the process of setting up the review is to specify which characteristics of the interventions (e.g. individual compounds of a drug), populations (e.g. acute and chronic conditions), outcomes (e.g. different depression measurement scales) and study designs, will be grouped together. Such decisions should be made independent of knowing which studies will be included and the methods of synthesis that will be used (e.g. meta-analysis). There may be a need to modify the comparisons and even add new ones at the review stage in light of the data that are collected. For example, important variations in the intervention may be discovered only after data are collected, or modifying the comparison may facilitate the possibility of synthesis when only one or few studies meet the comparison PICO. Planning for the latter scenario at the protocol stage may lead to less post-hoc decision making (Chapter 2, Section 2.5.4) and, of course, any changes made during the conduct of the review should be recorded and documented in the final report.

3.2 Articulating the review and comparison PICO

3.2.1 Defining types of participants: which people and populations?

The criteria for considering types of people included in studies in a review should be sufficiently broad to encompass the likely diversity of studies and the likely scenarios in which the interventions will be used, but sufficiently narrow to ensure that a meaningful answer can be obtained when studies are considered together; they should be specified in advance (see MECIR Box 3.2.a). As discussed in Chapter 2 (Section 2.3.1), the degree of breadth will vary, depending on the question being asked and the analytical approach to be employed. A range of evidence may inform the choice of population characteristics to examine, including theoretical considerations, evidence from other interventions that have a similar mechanism of action, and in vitro or animal studies. Consideration should be given to whether the population characteristic is at the level of the participant (e.g. age, severity of disease) or the study (e.g. care setting, geographical location), since this has implications for grouping studies and for the method of synthesis (Chapter 10, Section 10.11.5). It is often helpful to consider the types of people that are of interest in three steps.

MECIR Box 3.2.a: Relevant expectations for conduct of intervention reviews

First, the diseases or conditions of interest should be defined using explicit criteria for establishing their presence (or absence). Criteria that will force the unnecessary exclusion of studies should be avoided. For example, diagnostic criteria that were developed more recently – which may be viewed as the current gold standard for diagnosing the condition of interest – will not have been used in earlier studies. Expensive or recent diagnostic tests may not be available in many countries or settings, and time-consuming tests may not be practical in routine healthcare settings.

Second, the broad population and setting of interest should be defined. This involves deciding whether a specific population group is within scope, determined by factors such as age, sex, race, educational status or the presence of a particular condition such as angina or shortness of breath. Interest may focus on a particular setting such as a community, hospital, nursing home, chronic care institution, or outpatient setting. Box 3.2.a outlines some factors to consider when developing population criteria.

Whichever criteria are used for defining the population and setting of interest, it is common to encounter studies that only partially overlap with the review’s population. For example, in a review focusing on children, a cut-point of less than 16 years might be desirable, but studies may be identified with participants aged from 12 to 18. Unless the study reports separate data from the eligible section of the population (in which case data from the eligible participants can be included in the review), review authors will need a strategy for dealing with these studies (see MECIR Box 3.2.a). This will involve balancing concerns about reduced applicability by including participants who do not meet the eligibility criteria, against the loss of data when studies are excluded. Arbitrary rules (such as including a study if more than 80% of the participants are under 16) will not be practical if detailed information is not available from the study. A less stringent rule, such as ‘the majority of participants are under 16‘ may be sufficient. Although there is a risk of review authors’ biases affecting post-hoc inclusion decisions (which is why many authors endeavour to pre-specify these rules), this may be outweighed by a common-sense strategy in which eligibility decisions keep faith with the objectives of the review rather than with arbitrary rules. Difficult decisions should be documented in the review, checked with the advisory group (if available, see Chapter 1), and sensitivity analyses can assess the impact of these decisions on the review’s findings (see Chapter 10, Section 10.14 and MECIR Box 3.2.b).

Box 3.2.a: Factors to consider when developing criteria for ‘Types of participants’

MECIR Box 3.2.b Relevant expectations for conduct of intervention reviews

Third, there should be consideration of whether there are population characteristics that might be expected to modify the size of the intervention effects (e.g. different severities of heart failure). Identifying subpopulations may be important for implementation of the intervention. If relevant subpopulations are identified, two courses of action are possible: limiting the scope of the review to exclude certain subpopulations; or maintaining the breadth of the review and addressing subpopulations in the analysis.

Restricting the review with respect to specific population characteristics or settings should be based on a sound rationale. It is important that Cochrane Reviews are globally relevant, so the rationale for the exclusion of studies based on population characteristics should be justified. For example, focusing a review of the effectiveness of mammographic screening on women between 40 and 50 years old may be justified based on biological plausibility, previously published systematic reviews and existing controversy. On the other hand, focusing a review on a particular subgroup of people on the basis of their age, sex or ethnicity simply because of personal interests, when there is no underlying biologic or sociological justification for doing so, should be avoided, as these reviews will be less useful to decision makers and readers of the review.

Maintaining the breadth of the review may be best when it is uncertain whether there are important differences in effects among various subgroups of people, since this allows investigation of these differences (see Chapter 10, Section 10.11.5). Review authors may combine the results from different subpopulations in the same synthesis, examining whether a given subdivision explains variation (heterogeneity) among the intervention effects. Alternatively, the results may be synthesized in separate comparisons representing different subpopulations. Splitting by subpopulation risks there being too few studies to yield a useful synthesis (see Table 3.2.a and Chapter 2, Section 2.3.2). Consideration needs to be given to the subgroup analysis method, particularly for population characteristics measured at the participant level (see Chapters 10 and 26, (Fisher et al 2017)). All subgroup analyses should ideally be planned a priori and stated as a secondary objective in the protocol, and not driven by the availability of data.

In practice, it may be difficult to assign included studies to defined subpopulations because of missing information about the population characteristic, variability in how the population characteristic is measured across studies (e.g. variation in the method used to define the severity of heart failure), or because the study does not wholly fall within (or report the results separately by) the defined subpopulation. The latter issue mainly applies for participant characteristics but can also arise for settings or geographic locations where these vary within studies. Review authors should consider planning for these scenarios (see example reviews (Hetrick et al 2012, Safi et al 2017), Table 3.2.b, column 3).

Table 3.2.a Examples of population attributes and characteristics

3.2.2 Defining interventions and how they will be grouped

In some reviews, predefining the intervention (MECIR Box 3.2.c) may be straightforward. For example, in a review of the effect of a given anticoagulant on deep vein thrombosis, the intervention can be defined precisely. A more complicated definition might be required for a multicomponent intervention composed of dietary advice, training and support groups to reduce rates of obesity in a given population.

The inherent complexity present when defining an intervention often comes to light when considering how it is thought to achieve its intended effect and whether the effect is likely to differ when variants of the intervention are used. In the first example, the anticoagulant warfarin is thought to reduce blood clots by blocking an enzyme that depends on vitamin K to generate clotting factors. In the second, the behavioural intervention is thought to increase individuals’ self-efficacy in their ability to prepare healthy food. In both examples, we cannot assume that all forms of the intervention will work in the same way. When defining drug interventions, such as anticoagulants, factors such as the drug preparation, route of administration, dose, duration, and frequency should be considered. For multicomponent interventions (such as interventions to reduce rates of obesity), the common or core features of the interventions must be defined, so that the review authors can clearly differentiate them from other interventions not included in the review.

MECIR Box 3.2.c: Relevant expectations for conduct of intervention reviews

In general, it is useful to consider exactly what is delivered, who delivers it, how it is delivered, where it is delivered, when and how much is delivered, and whether the intervention can be adapted or tailored, and to consider this for each type of intervention included in the review (see the TIDieR checklist (Hoffmann et al 2014)). As argued in Chapter 17, separating interventions into ‘simple’ and ‘complex’ is a false dichotomy; all interventions can be complex in some ways. The critical issue for review authors is to identify the most important factors to be considered in a specific review. Box 3.2.b outlines some factors to consider when developing broad criteria for the ‘Types of interventions’ (and comparisons).

Box 3.2.b: Factors to consider when developing criteria for ‘Types of interventions’

Once interventions eligible for the review have been broadly defined, decisions should be made about how variants of the intervention will be handled in the synthesis. Differences in intervention characteristics across studies occur in all reviews. If these reflect minor differences in the form of the intervention used in practice (such as small differences in the duration or content of brief alcohol counselling interventions), then an overall synthesis can provide useful information for decision makers. Where differences in intervention characteristics are more substantial (such as delivery of brief alcohol counselling by nurses versus doctors), and are expected to have a substantial impact on the size of intervention effects, these differences should be examined in the synthesis. What constitutes an important difference requires judgement, but in general differences that alter decisions about how an intervention is implemented or whether the intervention is used or not are likely to be important. In such circumstances, review authors should consider specifying separate groups (or subgroups) to examine in their synthesis.

Clearly defined intervention groups serve two main purposes in the synthesis. First, the way in which interventions are grouped for synthesis (meta-analysis or other synthesis) is likely to influence review findings. Careful planning of intervention groups makes best use of the available data, avoids decisions that are influenced by study findings (which may introduce bias), and produces a review focused on questions relevant to decision makers. Second, the intervention groups specified in a protocol provide a standardized terminology for describing the interventions throughout the review, overcoming the varied descriptions used by study authors (e.g. where different labels are used for the same intervention, or similar labels used for different techniques) (Michie et al 2013). This standardization enables comparison and synthesis of information about intervention characteristics across studies (common characteristics and differences) and provides a consistent language for reporting that supports interpretation of review findings.3.2 A process for planning intervention groups for synthesis

3.2.3 Defining which comparisons will be made

When articulating the PICO for synthesis, defining the intervention groups alone is not sufficient for complete specification of the planned syntheses. The next step is to define the comparisons that will be made between the intervention groups. Setting aside for a moment more complex analyses such as network meta-analyses, which can simultaneously compare many groups (Chapter 11), standard meta-analysis (Chapter 10) aims to draw conclusions about the comparative effects of two groups at a time (i.e. which of two intervention groups is more effective?). These comparisons form the basis for the syntheses that will be undertaken if data are available. Cochrane Reviews sometimes include one comparison, but most often include multiple comparisons. Three commonly identified types of comparisons include the following. (Davey et al 2011)

• Intervention versus placebo (e.g. placebo drug, sham surgical procedure, psychological placebo). Placebos are most commonly used in the evaluation of pharmacological interventions, but may be also be used in some non-pharmacological evaluations. For example:
• newer generation antidepressants versus placebo (Hetrick et al 2012); and
• vertebroplasty for osteoporotic vertebral compression fractures versus placebo (sham procedure) (Buchbinder et al 2018).
• Intervention versus control (e.g. no intervention, wait-list control, usual care). Both intervention arms may also receive standard therapy. For example:
• chemotherapy or targeted therapy plus best supportive care (BSC) versus BSC for palliative treatment of esophageal and gastroesophageal-junction carcinoma (Janmaat et al 2017); and
• personalized care planning versus usual care for people with long-term conditions (Coulter et al 2015).
• Intervention A versus intervention B. A comparison of active interventions may include comparison of the same intervention delivered at different time points, for different lengths of time or different doses, or two different interventions. For example:
• early (commenced at less than two weeks of age) versus late (two weeks of age or more) parenteral zinc supplementation in term and preterm infants (Taylor et al 2017);
• high intensity versus low intensity physical activity or exercise in people with hip or knee osteoarthritis (Regnaux et al 2015);
• multimedia education versus other education for consumers about prescribed and over the counter medications (Ciciriello et al 2013).

The first two types of comparisons aim to establish the effectiveness of an intervention, while the last aims to compare the effectiveness of two interventions. However, the distinction between the placebo and control is often arbitrary, since any differences in the care provided between trials with a control arm and those with a placebo arm may be unimportant, especially where ‘usual care’ is provided to both. Therefore, placebo and control groups may be determined to be similar enough to be combined for synthesis.

In reviews including multiple intervention groups, many comparisons are possible. In some of these reviews, authors seek to synthesize evidence on the comparative effectiveness of all their included interventions, including where there may be only indirect comparison of some interventions across the included studies (Chapter 11, Section 11.2.1). However, in many reviews including multiple intervention groups, a limited subset of the possible comparisons will be selected. The chosen subset of comparisons should address the most important clinical and research questions. For example, if an established intervention (or dose of an intervention) is used in practice, then the synthesis would ideally compare novel or alternative interventions to this established intervention, and not, for example, to no intervention.

3.2.3.1 Dealing with co-interventions

Planning is needed for the special case where the same supplementary intervention is delivered to both the intervention and comparator groups. A supplementary intervention is an additional intervention delivered alongside the intervention of interest, such as massage in a review examining the effects of aromatherapy (i.e. aromatherapy plus massage versus massage alone). In many cases, the supplementary intervention will be unimportant and can be ignored. In other situations, the effect of the intervention of interest may differ according to whether participants receive the supplementary therapy. For example, the effect of aromatherapy among people who receive a massage may differ from the effect of the aromatherapy given alone. This will be the case if the intervention of interest interacts with the supplementary intervention leading to larger (synergistic) or smaller (dysynergistic/antagonistic) effects than the intervention of interest alone (Squires et al 2013). While qualitative interactions are rare (where the effect of the intervention is in the opposite direction when combined with the supplementary intervention), it is possible that there will be more variation in the intervention effects (heterogeneity) when supplementary interventions are involved, and it is important to plan for this. Approaches for dealing with this in the statistical synthesis may include fitting a random-effects meta-analysis model that encompasses heterogeneity (Chapter 10, Section 10.10.4), or investigating whether the intervention effect is modified by the addition of the supplementary intervention through subgroup analysis (Chapter 10, Section 10.11.2).

3.2.4 Selecting, prioritizing and grouping review outcomes

3.2.4.1 Selecting review outcomes

Broad outcome domains are decided at the time of setting up the review PICO (see Chapter 2). Once the broad domains are agreed, further specification is required to define the domains to facilitate reporting and synthesis (i.e. the PICO for comparison) (see Chapter 2, Section 2.4.3). The process for specifying and grouping outcomes largely parallels that used for specifying intervention groups.

Reporting of outcomes should rarely determine study eligibility for a review. In particular, studies should not be excluded because they do not report results of an outcome they may have measured, or provide ‘no usable data’ (MECIR Box 3.2.d). This is essential to avoid bias arising from selective reporting of findings by the study authors (see Chapter 13). However, in some circumstances, the measurement of certain outcomes may be a study eligibility criterion. This may be the case, for example, when the review addresses the potential for an intervention to prevent a particular outcome, or when the review addresses a specific purpose of an intervention that can be used in the same population for different purposes (such as hormone replacement therapy, or aspirin).

MECIR Box 3.2.d: Relevant expectations for conduct of intervention reviews

In general, systematic reviews should aim to include outcomes that are likely to be meaningful to the intended users and recipients of the reviewed evidence. This may include clinicians, patients (consumers), the general public, administrators and policy makers. Outcomes may include survival (mortality), clinical events (e.g. strokes or myocardial infarction), behavioural outcomes (e.g. changes in diet, use of services), patient-reported outcomes (e.g. symptoms, quality of life), adverse events, burdens (e.g. demands on caregivers, frequency of tests, restrictions on lifestyle) and economic outcomes (e.g. cost and resource use). It is critical that outcomes used to assess adverse effects as well as outcomes used to assess beneficial effects are among those addressed by a review (see Chapter 19).

Outcomes that are trivial or meaningless to decision makers should not be included in Cochrane Reviews. Inclusion of outcomes that are of little or no importance risks overwhelming and potentially misleading readers. Interim or surrogate outcomes measures, such as laboratory results or radiologic results (e.g. loss of bone mineral content as a surrogate for fractures in hormone replacement therapy), while potentially helpful in explaining effects or determining intervention integrity (see Chapter 5, Section 5.3.4.1), can also be misleading since they may not predict clinically important outcomes accurately. Many interventions reduce the risk for a surrogate outcome but have no effect or have harmful effects on clinically relevant outcomes, and some interventions have no effect on surrogate measures but improve clinical outcomes.

Various sources can be used to develop a list of relevant outcomes, including input from consumers and advisory groups (see Chapter 2), the clinical experiences of the review authors, and evidence from the literature (including qualitative research about outcomes important to those affected (see Chapter 21)). A further driver of outcome selection is consideration of outcomes used in related reviews. Harmonization of outcomes across reviews addressing related questions facilitates broader evidence synthesis questions being addressed through the use of Overviews of reviews (see online Chapter V).

Outcomes considered to be meaningful, and therefore addressed in a review, may not have been reported in the primary studies. For example, quality of life is an important outcome, perhaps the most important outcome, for people considering whether or not to use chemotherapy for advanced cancer, even if the available studies are found to report only survival (see Chapter 18). A further example arises with timing of the outcome measurement, where time points determined as clinically meaningful in a review are not measured in the primary studies. Including and discussing all important outcomes in a review will highlight gaps in the primary research and encourage researchers to address these gaps in future studies.

3.2.4.2 Prioritizing review outcomes

Once a full list of relevant outcomes has been compiled for the review, authors should prioritize the outcomes and select the outcomes of most relevance to the review question. The GRADE approach to assessing the certainty of evidence (see Chapter 14) suggests that review authors separate outcomes into those that are ‘critical’, ‘important’ and ‘not important’ for decision making.

The critical outcomes are the essential outcomes for decision making, and are those that would form the basis of a ‘Summary of findings’ table or other summary versions of the review, such as the Abstract or Plain Language Summary. ‘Summary of findings’ tables provide key information about the amount of evidence for important comparisons and outcomes, the quality of the evidence and the magnitude of effect (see Chapter 14, Section 14.1). There should be no more than seven outcomes included in a ‘Summary of findings’ table, and those outcomes that will be included in summaries should be specified at the protocol stage. They should generally not include surrogate or interim outcomes. They should not be chosen on the basis of any anticipated or observed magnitude of effect, or because they are likely to have been addressed in the studies to be reviewed. Box 3.2.c summarizes the principal factors to consider when selecting and prioritizing review outcomes.

Box 3.2.c: Factors to consider when selecting and prioritizing review outcomes

3.2.4.3 Defining and grouping outcomes for synthesis

Table 3.2.c outlines a process for planning for the diversity in outcome measurement that may be encountered in the studies included in a review and which can complicate, and sometimes prevent, synthesis. Research has repeatedly documented inconsistency in the outcomes measured across trials in the same clinical areas (Harrison et al 2016, Williamson et al 2017). This inconsistency occurs across all aspects of outcome measurement, including the broad domains considered, the outcomes measured, the way these outcomes are labelled and defined, and the methods and timing of measurement. For example, a review of outcome measures used in 563 studies of interventions for dementia and mild cognitive impairment found that 321 unique measurement methods were used for 1278 assessments of cognitive outcomes (Harrison et al 2016). Initiatives like COMET (Core Outcome Measures in Effectiveness Trials) aim to encourage standardization of outcome measurement across trials (Williamson et al 2017), but these initiatives are comparatively new and review authors will inevitably encounter diversity in outcomes across studies.

The process begins by describing the scope of each outcome domain in sufficient detail to enable outcomes from included studies to be categorized (Table 3.2.c Step 1). This step may be straightforward in areas for which core outcome sets (or equivalent systems) exist (Table 3.2.c Step 2). The methods and timing of outcome measurement also need to be specified, giving consideration to how differences across studies will be handled (Table 3.2.c Steps 3 and 4). Subsequent steps consider options for dealing with studies that report multiple measures within an outcome domain (Table 3.2.c Step 5), planning how outcome domains will be used in synthesis (Table 3.2.c Step 6), and building in contingencies to maximize potential to synthesize (Table 3.2.c Step 7).

Table 3.2.c A process for planning outcome groups for synthesis

3.3 Determining which study designs to include

Some study designs are more appropriate than others for answering particular questions. Authors need to consider a priori what study designs are likely to provide reliable data with which to address the objectives of their review (MECIR Box 3.3.a). Sections 3.3.1 and 3.3.2 cover randomized and non-randomized designs for assessing treatment effects; Chapter 17 (Section 17.2.5) discusses other study designs in the context of addressing intervention complexity.

MECIR Box 3.3.a: Relevant expectations for conduct of intervention reviews

3.3.1 Including randomized trials

Because Cochrane Reviews address questions about the effects of health care, they focus primarily on randomized trials and randomized trials should be included if they are feasible for the interventions of interest (MECIR Box 3.3.b). Randomization is the only way to prevent systematic differences between baseline characteristics of participants in different intervention groups in terms of both known and unknown (or unmeasured) confounders (see Chapter 8), and claims about cause and effect can be based on their findings with far more confidence than almost any other type of study. For clinical interventions, deciding who receives an intervention and who does not is influenced by many factors, including prognostic factors. Empirical evidence suggests that, on average, non-randomized studies produce effect estimates that indicate more extreme benefits of the effects of health care than randomized trials. However, the extent, and even the direction, of the bias is difficult to predict. These issues are discussed at length in Chapter 24, which provides guidance on when it might be appropriate to include non-randomized studies in a Cochrane Review.

Practical considerations also motivate the restriction of many Cochrane Reviews to randomized trials. In recent decades there has been considerable investment internationally in establishing infrastructure to index and identify randomized trials. Cochrane has contributed to these efforts, including building up and maintaining a database of randomized trials, developing search filters to aid their identification, working with MEDLINE to improve tagging and identification of randomized trials, and using machine learning and crowdsourcing to reduce author workload in identifying randomized trials (Chapter 4, Section 4.6.6.2). The same scale of organizational investment has not (yet) been matched for the identification of other types of studies. Consequently, identifying and including other types of studies may require additional efforts to identify studies and to keep the review up to date, and might increase the risk that the result of the review will be influenced by publication bias. This issue and other bias-related issues that are important to consider when defining types of studies are discussed in detail in Chapters 7 and 13.

Specific aspects of study design and conduct should be considered when defining eligibility criteria, even if the review is restricted to randomized trials. For example, whether cluster-randomized trials (Chapter 23, Section 23.1) and crossover trials (Chapter 23, Section 23.2) are eligible, as well as other criteria for eligibility such as use of a placebo comparison group, evaluation of outcomes blinded to allocation sequence, or a minimum period of follow-up. There will always be a trade-off between restrictive study design criteria (which might result in the inclusion of studies that are at low risk of bias, but very few in number) and more liberal design criteria (which might result in the inclusion of more studies, but at a higher risk of bias). Furthermore, excessively broad criteria might result in the inclusion of misleading evidence. If, for example, interest focuses on whether a therapy improves survival in patients with a chronic condition, it might be inappropriate to look at studies of very short duration, except to make explicit the point that they cannot address the question of interest.

MECIR Box 3.3.b: Relevant expectations for conduct of intervention reviews

3.3.2 Including non-randomized studies

The decision of whether non-randomized studies (and what type) will be included is decided alongside the formulation of the review PICO. The main drivers that may lead to the inclusion of non-randomized studies include: i) when randomized trials are unable to address the effects of the intervention on harm and long-term outcomes or in specific populations or settings; or (ii) for interventions that cannot be randomized (e.g. policy change introduced in a single or small number of jurisdictions) (see Chapter 24). Cochrane, in collaboration with others, has developed guidance for review authors to support their decision about when to look for and include non-randomized studies Schunemann et al 2013.

Non-randomized designs have the commonality of not using randomization to allocate units to comparison groups, but their different design features mean that they are variable in their susceptibility to bias. Eligibility criteria should be based on explicit study design features, and not the study labels applied by the primary researchers (e.g. case-control, cohort), which are often used inconsistently ((Reeves et al 2017), Chapter 24).

When non-randomized studies are included, review authors should consider how the studies will be grouped and used in the synthesis. The Cochrane Non-randomized Studies Methods Group taxonomy of design features (see Chapter 24) may provide a basis for grouping together studies that are expected to have similar inferential strength and for providing a consistent language for describing the study design.

Once decisions have been made about grouping study designs, planning of how these will be used in the synthesis is required. Review authors need to decide whether it is useful to synthesize results from non-randomized studies and, if so, whether results from randomized trials and non-randomized studies should be included in the same synthesis (for the purpose of examining whether study design explains heterogeneity among the intervention effects), or whether the effects should be synthesized in separate comparisons (Valentine and Thompson 2013). Decisions should be made for each of the different types of non-randomized studies under consideration. Review authors might anticipate increased heterogeneity when non-randomized studies are synthesized, and adoption of a meta-analysis model that encompasses heterogeneity is wise (Valentine and Thompson 2013) (such as a random effects model, see Chapter 10, Section 10.10.4). For further discussion of non-randomized studies, see Chapter 24.

3.4 Eligibility based on publication status and language

Chapter 4 contains detailed guidance on how to identify studies from a range of sources including, but not limited to, those in peer-reviewed journals. In general, a strategy to include studies reported in all types of publication will reduce bias (Chapter 7). There would need to be a compelling argument for the exclusion of studies on the basis of their publication status (MECIR Box 3.4.a), including unpublished studies, partially published studies, and studies published in ‘grey’ literature sources. Given the additional challenge in obtaining unpublished studies, it is possible that any unpublished studies identified in a given review may be an unrepresentative subset of all the unpublished studies in existence. However, the bias this introduces is of less concern than the bias introduced by excluding all unpublished studies, given what is known about the impact of reporting biases (see Chapter 13 on bias due to missing studies, and Chapter 4, Section 4.3 for a more detailed discussion of searching for unpublished and grey literature).

Likewise, while searching for, and analysing, studies in any language can be extremely resource-intensive, review authors should consider carefully the implications for bias (and equity, see Chapter 16) if they restrict eligible studies to those published in one specific language (usually English). See Chapter 4 (Section 4.4.5) for further discussion of language and other restrictions while searching.

MECIR Box 3.4.a: Relevant expectations for conduct of intervention reviews

3.5 Chapter information

Authors: Joanne E McKenzie, Sue E Brennan, Rebecca E Ryan, Hilary J Thomson, Renea V Johnston, James Thomas

Acknowledgements: This chapter builds on earlier versions of the Handbook. In particular, Chapter 5, edited by Denise O’Connor, Sally Green and Julian Higgins.

Funding: JEM is supported by an Australian National Health and Medical Research Council (NHMRC) Career Development Fellowship (1143429). SEB and RER’s positions are supported by the NHMRC Cochrane Collaboration Funding Program. HJT is funded by the UK Medical Research Council (MC_UU_12017-13 and MC_UU_12017-15) and Scottish Government Chief Scientist Office (SPHSU13 and SPHSU15). RVJ’s position is supported by the NHMRC Cochrane Collaboration Funding Program and Cabrini Institute. JT is supported by the National Institute for Health Research (NIHR) Collaboration for Leadership in Applied Health Research and Care North Thames at Barts Health NHS Trust. The views expressed are those of the author(s) and not necessarily those of the NHS, the NIHR or the Department of Health.

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