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Cochrane Database of Systematic Reviews Protocol - Intervention

Dopamine agonists for traumatic brain injury

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Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To assess the efficacy and safety of dopamine agonists for adults with traumatic brain injury.

Background

Description of the condition

Traumatic brain injury (TBI) is a leading cause of death and disability following significant head injuries such as those sustained in road traffic accidents, falls, assaults, and sporting injuries (Park 2008). More than 50 million TBIs occur worldwide each year (Feigin 2013), with substantial worldwide variation in aetiology of injury and fatality rate (Li 2016). European epidemiological data estimate an aggregate hospitalised and fatal TBI incidence rate of 262 per 100,000 people per year (Peeters 2015; Tagliaferri 2006).

Recovery from TBI can be variable and unpredictable. Severe TBI can result in prolonged disorders of consciousness, with 40% to 70% of people who survive TBI experiencing long‐term neuropsychiatric complications including persistent cognitive deficits, social and behavioural complaints, and mood and behavioural disorders (Bales 2009; Bhalerao 2013; Fleminger 2008; Selassie 2008). The economic burden of TBI is substantial. The direct medical costs of TBI in the US were estimated as USD 80 billion in 2000, and indirect costs, such as lost productivity, totaled an estimated USD 326 billion (Corso 2006).

Little can be done after the event to prevent the deleterious effects of primary TBI, which is the damage to the brain sustained at the time of injury. However, secondary brain injury ‐ the damage and death of brain tissue in the hours to days after injury ‐ is a promising target for interventions aiming to reduce and prevent the cognitive changes of TBI by optimising neuronal metabolism, avoiding deleterious effects of raised intracranial pressure, and preventing inflammatory cytotoxicity. Neuroprotective drugs, which act by either interrupting the cascade of secondary injury or enhancing the recovery of function, have therefore long been considered a fruitful research area. Although mood disorders and episodes of psychosis respond well to similar therapies used for patients without brain injury, major problems remain in the management of behavioural disturbance and impaired cognitive function following TBI. Despite enormous research efforts focused on developing effective therapy, no pharmacologic agent has been demonstrated to improve functional outcomes following TBI (Beauchamp 2008).

Traumatic brain injury is thought to induce widespread damage to the dopaminergic system, resulting in dysfunction in animal models of cortical and subcortical regions including the hippocampus, striatum, and frontal cortex (Bales 2009; Missale 1998; Redell 2007; Shin 2011; Tate 2000). Furthermore, TBI has been shown to influence dopamine (DA) signalling, with deficits in dopamine 2 receptor (D₂R) and dopamine active transporter (DAT) activity demonstrated on neuroimaging of brain‐injured patients (Donnemiller 2000). Such dysfunction includes disruptions in glutamatergic cortico‐striatal projections and striatal gamma‐aminobutyric acid (GABA)ergic outputs (Bales 2009; Hinzman 2010; Missale 1998). The adverse effect on DA signalling following TBI is thought to be responsible for the significant neuropsychiatric sequelae observed, while disturbance of DA modulation and neurotransmission is thought to contribute directly to cognitive impairment and influence post‐traumatic recovery. Indeed, DA antagonists, such as the typical antipsychotic haloperidol, have been shown to impair neurological recovery in animal models of brain injury (Goldstein 1993), suggesting a role for DA agonists in enhancing and modulating neuronal recovery.

Description of the intervention

Dopamine is a monoamine neurotransmitter and neuromodulator involved in a number of physiological functions, including hormone secretion, movement control, motivation, emotion, and cognitive processing (Crosson 2003; Floresco 2006). Dopamine agonists are medications that stimulate DA receptors; they can act either by stimulating DA receptors directly, or indirectly by promoting the release of stored DA or preventing reuptake of DA at nerve terminals. Dopamine agonists are most commonly used in the early treatment of Parkinson's disease (Brooks 2000). The use of DA agonists such as amantadine can facilitate striatal DA release, increase the number of post‐synaptic DA receptors, stimulate dopa‐decarboxylase activity in the striatum, and alter DA receptors' conformation (Kraus 2005; Moresco 2002), all of which could potentially improve or normalise DA transmission in the injured, dysregulated brain.

In view of the stimulation of DA receptors (in addition some DA agonists are also reversible N‐methyl‐D‐aspartate (NMDA) glutamate receptor antagonists, which also enhance dopaminergic transmission) (Hesselink 1999; Kegeles 2002), it is hypothesised that these different activities may be beneficial in the treatment of TBI through their actions on the postinjury dysfunctional DA system. Although to date there are no accepted protocols for the use of DA agonists, and consequently no accepted dosing regimens or timing of introduction following TBI, several trials have considered their use at various points during rehabilitation from TBI, where normalising DA transmission may contribute to improving neurologic and attention deficits. The mechanism(s) of action of many centrally acting dopaminergic drugs, especially following TBI, remain largely unexplored, while the benefits and risks of these agents have not been established (Frenette 2012).

Attention deficits are commonly seen following TBI, during which phase the brain is thought to be attempting to 're‐learn' everyday skills (Sivan 2010). The use of drugs that enhance DA signalling in both the acute and chronic phases of TBI is intended to improve the ability of the brain to learn the tasks or to modify neuronal connections damaged during the initial acute phase of primary and early secondary brain injury. Such agents may work through simply driving these pathways to relieve dysfunction or by creating changes in neuronal plasticity.

Dopamine agonists currently in clinical use include: amantadine, apomorphine, bromocriptine, cabergoline, dihydroergotoxine, fenoldopam, levodopa, lisuride, methylphenidate, mesulergine, metergoline, pergolide, piribedil, pramipexol, quinagolide, quinpirole, ropinirole, rotigotine, and terguride.

How the intervention might work

There are a number of mechanisms of action for drugs that affect DA levels, from direct agonists at the dopamine receptor to reuptake inhibition which causes increased synaptic DA levels. These also carry variable receptor selectivity with regard to locality and pre/postsynaptic effects (Sivan 2010).

For example, methylphenidate has effects on a number of targets, and affects DA, serotonin, and noradrenaline levels. Methylphenidate is thought to exert its main effect by acting at DA reuptake transporters, where it blocks the reuptake of DA and therefore concentrates extracellular DA levels especially in the prefrontal cortex (Talsky 2011). In terms of clinical outcome, the aim of treatment with methylphenidate would be to improve attention and concentration in a similar way to the use of methylphenidate in people with attention deficit. However, not all attention deficit aspects of TBI respond to treatment with methylphenidate (Sivan 2010). So whilst the pharmacological rationale for treatment of TBI with drugs such as methylphenidate can be extrapolated from their primary uses, it must be acknowledged that the therapeutic effects of the drugs will not necessarily match the effects in comparison to their primary use. In the case of methylphenidate, its dopaminergic effect on TBI may be complicated by additional effects on noradrenaline and serotonin, which may in turn affect mood and agitation, particularly as the frontal lobes contain the greatest number of adrenergic and serotonergic fibres and are commonly damaged in TBI (Gualtieri 1988).

Amantadine is the most widely researched DA agonist in rehabilitation following TBI, with reports of its use improving cognitive function (Andersson 1992), attention (Nickels 1994), and motivation when used during rehabilitation (Kraus 1997). A case series of 30 participants demonstrated the effectiveness of amantadine in attenuating aggression in behaviourally disturbed brain‐injured patients (Gualtieri 1989), and open‐label trials of amantadine (Kraus 2005) and bromocriptine (Powell 1996) also showed improved neuropsychiatric outcomes following TBI. However, the action of amantadine on DA in the brain is perhaps least understood, as it may have both a direct and indirect action on DA neurons. At the presynaptic neuron DA receptors, amantadine increases DA release and inhibits reuptake, while at the postsynaptic neuron DA receptors the drug is thought to increase either DA receptor numbers or their sensitivity. In addition, a weak, non‐competitive effect on NMDA receptors by amantadine has been demonstrated, which may have some effect on alleviating glutamate excitotoxicity in TBI, thus restoring the balance between glutaminergic and dopaminergic systems (Bales 2011; Kraus 1997; Patrick 2006).

Why it is important to do this review

A review evaluating DA agonists as an intervention in treating TBI is important to determine whether DA agonists do mitigate morbidity and mortality due to attenuating or enhancing recovery from secondary brain injury. There is evidence that DA agonists can improve cognition following acute TBI in humans (Giacino 2012; McDowell 1998), as well as in animal models (Kihara 2002). Despite this, neuroprotective strategies have not been implemented in the clinical setting (Bales 2010).

In order to provide the best available evidence to guide good clinical practice for people with TBI, we intend to perform a systematic review of all randomised controlled trials of DA agonists for TBI. Two systematic reviews have failed to draw clear conclusions of efficacy due to the heterogeneity of outcome measures, and side effects were poorly explored (Frenette 2012; Sami 2015). We intend to broaden the search strategy to include trials registries and to update the searches undertaken by Sami 2015 in December 2013. We will investigate known sources of heterogeneity, characterise the side effects, and where possible the incidence of such side effects, of this class of drugs in the management of TBI. In addition, we have broadened our outcomes of interest to include mortality.

Objectives

To assess the efficacy and safety of dopamine agonists for adults with traumatic brain injury.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised controlled trials (RCTs), including those with an open‐label design. We will include reports of studies whether published or unpublished, except those published after 2010 for which we cannot access a registered protocol, in accordance with the policy of the Cochrane Injuries Group (Roberts 2015). We will not include cross‐over studies because we will be considering long‐term outcomes. Cluster‐randomised studies are unlikely to have been performed on this topic and will not be included.

Types of participants

We will include people aged 18 years and older with clinically diagnosed brain injury of unambiguously traumatic cause. We will include all severities of head injury: mild, moderate, or severe (according to the Glasgow Coma Score (GCS)) (Brain Trauma 2007). This includes any brain injury of traumatic aetiology that causes disturbance of consciousness and dysfunctions within six months of the initial trauma.

For trials including a subset of participants meeting our inclusion criteria (e.g. if a trial includes participants with other aetiology of brain injuries, such as secondary to hypoxia or cerebrovascular disease), we will attempt to use only the outcome data for the traumatic subset of participants by contacting the authors for this information. If for whatever reason these data are not available, we will only include the study in the review if the proportion of TBI participants is above 50%, with the ratio of TBI to other participants included in the 'Characteristics of included studies' table for each study. If we are unable to obtain the disaggregated data and the proportion of TBI participants remains unclear, we will include the study in the review but leave the data out of the meta‐analyses.

Types of interventions

We will include trials assessing the following comparisons.

  1. Any DA agonist versus placebo

  2. Any DA agonist plus usual care versus usual care alone

We will check to ensure that usual care, including non‐pharmacological rehabilitative therapy, was provided equally to people in both arms of all included studies.

Types of outcome measures

Primary outcomes

  1. All‐cause mortality.

  2. Functional outcomes (i.e. degree of rehabilitation and residual disability) measured using a validated scale such as the Disability Rating Scale (DRS) (Wright 2000), the Glasgow Outcome Scale (GOS) (Jennett 1975), or Extended Glasgow Outcome Scale (GOS‐E) (Jennett 1981).

Secondary outcomes

  1. Duration of post‐traumatic amnesia, as assessed by the Galveston Orientation and Amnesia Test or comparable scales (Levin 1979).

  2. Cognitive functioning, measured using any validated neuropsychological scales including the following (Tsaousides 2009):

    1. intellectual function (e.g. Wechsler Adult Intelligence Scale III (WAIS‐III), Wechsler Abbreviated Scale of Intelligence);

    2. executive function (e.g. Behavioural Assessment of the Dysexecutive Syndrome, Delis‐Kaplan Executive Function System, Category Test, Stroop Test, Wisconsin Card Sorting Test);

    3. processing speed (e.g. WAIS‐III (Digital Symbol‐Coding and Symbol Search subtests), Woodcock‐Johnson Test of Cognitive Abilities (Decision Speed and Visual Match subtests), Stroop Colour Word Test, Trail Making Test);

    4. psychomotor speed (e.g. Fingertapping Test, Grooved Pegboard, Purdue Pegboard);

    5. attention (e.g. Conner's Continuous Performance Test, Symbol Digit Modalities Test, Paced Auditory Serial Attention Test, WAIS‐IV (Digit Span and Letter‐Number Sequencing subtests));

    6. language (e.g. Boston Naming Test, Peabody Picture Vocabulary Test, Controlled Oral Word Association Tests, Multilingual Aphasia Examination, Boston Diagnostic Aphasia Examination);

    7. memory (e.g. Wechsler Memory Scale, California Verbal Learning Test, Hopkins Verbal Learning Test, Rey Auditory Verbal Learning Test, Benton Visual Retention Test, Rey‐Osterrieth Complex Figure Test).

  3. Cognitive impairment. We will use a dichotomised method to define the presence of cognitive impairment, e.g. having the Modified Mini‐Mental State Examination or Telephone Interview for Cognitive Status scores (Folstein 1975; Knopman 2010).

  4. Adverse events (medical occurrence temporally associated with the use of a medicinal product, but not necessarily causally related) as reported in the included studies.

  5. Side effects (unintended effect occurring at normal dose related to the pharmacological properties) as reported in the included studies.

We will assess primary and secondary outcomes at one to three months after the injury (short term); three to less than six months (medium term); and six months or longer (long term). Failure to report one or more of the outcomes listed will not be an exclusion criterion for this review. We chose at least one month for short‐term follow‐up, as many studies in intensive care start with a delay of a month; if the injury was terminal most deaths will have occurred by this point. Where identical outcomes are reported but differ in time to follow‐up, we will assess this within subgroup analyses.

To determine the optimal information size for the all‐cause mortality outcome, we assumed a 20% risk in the control group and a 20% relative risk reduction, with 90% power and a statistical significance level of 0.05. The optimal information size needed to reliably detect a plausible treatment effect in mortality, using a two‐sample, two‐sided equality test, is 1,212 people.

For the disability outcome, we assumed a 25% risk in the control group (of a representative GOS of 1 to 3) and a 20% relative risk reduction, with 90% power and a significance level of 0.05. The optimal information size needed to reliably detect a plausible treatment effect in disability is 1,464 people.

Search methods for identification of studies

In order to reduce publication and retrieval bias, we will not restrict our search by language, date or publication status.

Electronic searches

The Cochrane Injuries Group's Information Specialist will conduct searches in the following databases for RCTs and controlled clinical trials. There will be no language or publication year restrictions.

  1. Cochrane Central Register of Controlled Trials (which contains the Cochrane Injuries Trials Register) in the Cochrane Library (latest issue)

  2. Ovid MEDLINE(R), Ovid MEDLINE(R) In‐Process & Other Non‐Indexed Citations, Ovid MEDLINE(R) Daily and Ovid OLDMEDLINE(R) (1946 to present)

  3. Embase Classic + Embase (OvidSP) (1947 to present)

  4. ISI Web of Science: Science Citation Index Expanded (SCI‐EXPANDED) (1970 to present)

  5. ISI Web of Science: Conference Proceedings Citation Index‐Science (CPCI‐S) (1990 to present)

  6. ClinicalTrials.gov (www.clinicaltrials.gov)

  7. World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) (apps.who.int/trialsearch)

The Information Specialist will adapt the MEDLINE search strategy illustrated in Appendix 1 as necessary for the other databases, including the RCT filter, which is a modified version of the Cochrane Highly Sensitive Search Strategies (Lefebvre 2011).

Searching other resources

We will search the reference lists of all included studies and reviews.

Data collection and analysis

Selection of studies

Two review authors (NRP and SL) will independently screen the titles, abstracts, and keywords of citations obtained from the search of the electronic databases and exclude studies that do not fulfil the inclusion criteria. We will obtain full‐text reports of potentially eligible studies and studies for which the abstract provided insufficient information to determine eligibility. Two review authors will screen the full‐text reports for inclusion in the review. Any disagreements will be resolved by discussion, or through discussion with a third review author (CM) where necessary. We will examine all included studies to verify that they present unique datasets. If individual trials are reported in multiple papers, results will be assembled by trial ID and maximal data extracted. Duplicate results will be excluded if this is not possible.

We will record reasons for the exclusion of any study assessed at the full‐text stage and report key excluded studies in a 'Characteristics of excluded studies' table. We will agree on a hierarchy of reasons for study exclusion based on the inclusion criteria and will record the reason for exclusion as the first criterion not met. We will identify and exclude duplicates, and collate multiple reports of the same study so that each study, rather than each report, is the unit of interest in the review.

Data extraction and management

Two review authors (NRP and SL) will independently extract data from the included studies and record the information on a data collection form. We will extract the following data.

  1. General information about the article including authors and year of publication.

  2. Methods: study design, total duration of study, study location, study setting, date of study, methods of statistical analysis.

  3. Participants: age, gender, severity of TBI, diagnostic criteria if applicable, inclusion and exclusion criteria, similarity of groups at baseline, withdrawals.

  4. Interventions: description of intervention, comparison, duration, route of administration, with or without other combined non‐standard treatment.

  5. Outcomes: description of primary and secondary outcomes specified and collected, and time points reported.

  6. Information relevant to 'Risk of bias' assessments including sequence generation, allocation concealment, loss to follow‐up, blinding of personnel, participants, and outcome assessors, and the likelihood of selective outcome reporting.

  7. Notes: funding for the trial, details of ethical committee approval, details of prospective study registration, and notable conflicts of interest of trial authors.

We will request unpublished information from the study authors where necessary. Data extraction by each review author will be compared and any disagreements resolved through discussion or arbitration with a third review author (CM).

Assessment of risk of bias in included studies

Two review authors (NRP and SL) will independently assess the risk of bias of included studies using the 'Risk of bias' assessment tool described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will evaluate the risk of bias by assessing the following.

  • Random sequence generation (checking for possible selection bias). We plan to assess the method used to generate the allocation sequence as: low risk of bias (any truly random process, e.g. random number table; computer random number generator); unclear risk of bias (method used to generate sequence not clearly stated). We will exclude studies using a non‐random process (e.g. odd or even date of birth; hospital or clinic record number).

  • Allocation concealment (checking for possible selection bias). The method used to conceal allocation to interventions prior to assignment determines whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment. We will assess the methods as: low risk of bias (e.g. telephone or central randomisation; consecutively numbered, sealed, opaque envelopes); unclear risk of bias (method not clearly stated). We will exclude studies that did not conceal allocation (e.g. open list).

  • Blinding of participants and personnel (checking for possible performance bias). We will assess the methods used to blind study participants and personnel from knowledge of which intervention a participant received. We will assess methods as: low risk of bias (study states that it was blinded and describes the method used to achieve blinding, such as identical tablets matched in appearance or smell, or a double‐dummy technique); unclear risk of bias (study states that it was blinded but does not provide an adequate description of how this was achieved). We will consider studies that are not double‐blind to be at high risk of bias.

  • Blinding of outcome assessment (checking for possible detection bias). We aim to assess the methods used to blind study participants and outcome assessors from knowledge of which intervention a participant received. We will assess the methods as: low risk of bias (study has a clear statement that outcome assessors were unaware of treatment allocation, and ideally describes how this was achieved); unclear risk of bias (study states that outcome assessors were blind to treatment allocation but lacks a clear statement on how this was achieved). We will consider studies where outcome assessment was not blinded as being at high risk of bias.

  • Selective reporting (checking for reporting bias). We will assess whether primary and secondary outcome measures were prespecified and whether these were consistent with those reported. We will assess selective reporting as: low risk of bias (studies reporting primary and secondary outcomes); high risk of bias (not all prespecified outcomes were reported or were only reported for certain data collection time points).

  • Incomplete outcome data (checking for possible attrition bias due to the amount, nature, and handling of incomplete outcome data). We aim to assess the methods used to deal with incomplete data as: low risk (< 10% of participants did not complete the study and/or ‘baseline observation carried forward’ analysis was used); unclear risk of bias ('last observation carried forward' analysis was used); high risk of bias ('completer' analysis was used).

We will create a 'Risk of bias' table including our judgement of 'low risk', 'high risk', or 'unclear risk' of bias for each trial for each domain. The two review authors will resolve any disagreements through discussion or through arbitration involving a third review author. For each study we will provide summary statements to support our judgement, and where possible we will provide a quote from the study as further justification. We will summarise risk of bias across all studies for each type of bias.

Measures of treatment effect

We will pool outcomes by scales used, based on specific neuropsychiatric outcome measurements. Where possible, we will make comparisons between scales used (e.g. between alternative measures of functional recovery). Most scores are likely to be final outcomes, but some may be changes from baseline (e.g. GCS); we will handle these as separate analyses.

We will conduct analyses using data adjusted for baseline as opposed to unadjusted analyses. We will conduct an intention‐to‐treat analysis, as opposed to a per‐protocol analysis.

We will calculate the pooled risk ratio (RR) and 95% confidence interval (CI) for dichotomous data. For continuous data, we will use pooled mean difference (MD), or, where outcome data are reported on different scales that measure similar concepts, we will use standardised pooled mean difference (SMD) and 95% CI, back transforming the SMD to a familiar scale selected from a study included in the original meta‐analysis that is representative of the population and intervention and is at low risk of bias.

We will pool findings for the two primary outcomes and for the secondary outcomes of post‐traumatic amnesia and adverse events and side effects, where similar events are reported. For the remaining secondary outcomes of cognitive functioning and cognitive impairment, we will not pool data, as neuropsychiatric tests are validated for specific functions that are not open to generalisation.

Unit of analysis issues

The unit of analysis will be the individual participant.

For studies with multiple treatment groups, in the primary analysis we will combine results across all eligible interventions and compare them with the combined results across all eligible control groups, making single, pair‐wise comparisons. We will do this only if interventions are considered sufficiently similar. Where interventions are not considered sufficiently similar to combine, we will analyse each 'arm' of the trial separately (against a common control group), but divide the sample size for common comparator groups proportionately across each comparison (Higgins 2008). This simple approach will allow use of standard software (including Review Manager 5) (RevMan 2014), and prevent inappropriate double‐counting of participants.

Dealing with missing data

If data are missing from published reports, we will attempt to contact study authors to obtain this information. In the case of missing outcome data, we will only analyse the data that are available in the publication (i.e. we will not impute further). We will consider the potential impact of the missing data during the interpretation of the results.

Assessment of heterogeneity

We will examine statistical heterogeneity with visual inspection of the forest plot and taking into consideration the magnitude and direction of effect, as well as the I² statistic and Chi² test. We will consider substantial heterogeneity to exist with I² values greater than 80% and Chi² test P values less than 0.1. If there is substantial heterogeneity, we will assess heterogeneity by careful examination of the study reports and by using the preplanned subgroup analyses. We will consider whether it is appropriate to do a meta‐analysis, particularly if the direction of effect is inconsistent.

Assessment of reporting biases

To investigate the possibility of reporting biases, including publication bias, we will draw funnel plots (Egger 1997). Any asymmetry present might be due to publication bias, but might also be caused by a genuine relationship between trial size and effect size. We will examine clinical variation of the studies to explore asymmetry and will also compare results extracted from published journal reports with results obtained from other sources (e.g. trial protocols). We will only produce funnel plots if there is a minimum of 10 studies in any meta‐analysis.

Data synthesis

We will calculate the pooled RRs and 95% CIs for dichotomous outcomes, and the pooled MDs or SMD and 95% CIs for continuous outcomes using a random‐effects model. We have chosen a random‐effects model as we assume that there will be clinical and methodological differences between the included studies. We will test these assumptions by undertaking sensitivity analyses using a fixed‐effect model.

When using change from baseline score, we will follow the advice of the Cochrane Handbook for Systematic Reviews of Interventions in producing a meta‐analysis of mean differences (Deeks 2011). We will perform all analyses using Review Manager 5 (RevMan 2014). We will perform meta‐analysis if two or more studies assess the same outcome. If meta‐analysis is not possible, we will report study findings narratively.

Subgroup analysis and investigation of heterogeneity

Where there are sufficient data, we intend to perform the following subgroup analyses to account for clinical heterogeneity.

  1. Severity of brain injury: severe TBI (GCS ≦ 8) versus moderate TBI (GCS 9 to 12) versus mild TBI (GCS 13 to 15).

  2. Type of DA agonist (direct or indirectly acting), or individual drug if sufficient trials (at least three) are available.

  3. Dose of DA agonist (high versus low, for specific drug).

  4. Length of treatment: from one month but less than three months (short term); three months but less than six months (medium term); six months or longer (long term).

Sensitivity analysis

We will conduct sensitivity analyses to quantify differential effects (if any) when trials that we have assessed as at high risk of bias (with regard to the methods used to generate and conceal the randomisation sequence) are excluded. We will use Trial Sequential Analysis methods to explore any statistically significant effect found where the outcome did not meet the expected sample size.

Quality of the evidence

Two review authors will independently assess the quality of the evidence for all outcomes using the GRADE approach (Schünemann 2013). Using the GRADE approach, we will assess the quality of the body of evidence with reference to the methodological quality of each study, directness of the evidence (generalisability), consistency of the results (heterogeneity), precision of effect estimates, and risk of publication bias. We will rate the quality of each body of evidence as 'high', 'moderate', 'low', or 'very low' and will justify our decisions.

We plan to decrease the GRADE rating by one (‐1) or two (‐2) if we identify:

  • serious (‐1) or very serious (‐2) limitation to study quality;

  • important inconsistency (‐1);

  • some (‐1) or major (‐2) uncertainty about directness;

  • imprecise or sparse data (‐1);

  • high probability of reporting bias (‐1).

'Summary of findings' table

We will produce a 'Summary of findings' table for each comparison and for all primary and secondary outcomes, presenting the main findings of our review in a simple tabular form. For both comparisons, we will use the groups not receiving DA treatment to calculate the assumed risk. In the table we will present information regarding the quality of the evidence and the magnitude of any effect of the interventions, using GRADE as described above. We will use the GRADEpro Guideline Development Tool software to produce the 'Summary of findings' table (GRADEpro 2015). We will construct the 'Summary of findings' table following analysis of our results and prior to writing up our Results and Discussion.