Primary outcomes

Secondary outcomes

• Change in subjective evaluation of clinical status evaluated by both patients and clinicians, as assessed with validated assessment tools such as the Patient Subjective Assessment of Change, Patient Global Assessment of Improvement, Patient Evaluation of Global Response (PEGR), Patient and Physician Global Assessment of Change, Investigator Global Assessment of Efficacy (IGAE), Physician Global Assessment of Change (PGAC), and visual analogue scale (VAS) for symptom severity, measured between weeks 3 and 6 post‐injection.

• Changes in pain scores, as assessed with validated assessment tools such as the Patient Assessment of Pain, TWSTRS‐pain sub‐scale score, and VAS Pain score, measured between weeks 2 and 6 post‐injection.

• Changes in quality of life assessments, as assessed with validated assessment tools such as the Short Form 36 (SF‐36) quality‐of‐life questionnaire, measured at any point during study follow‐up.

• Numbers of participants with adverse events of special interest, such as dysphagia, sore throat, and local injection‐site pain, measured at any point during study follow‐up.

• Duration of effect, assessed by the number of days until need for reinjection or effect waning.

Databases searched

• Cochrane Movement Disorders Group trials register (June 2003);

• Cochrane Central Register of Controlled Trials (CENTRAL; the Cochrane Library 2016, Issue 11);

• MEDLINE (1977 to 6 October 2016);

• Embase (1977 to 6 October 2016).

Random sequence generation

• Low risk of bias: the study performed sequence generation using computer random number generation or a random number table. Drawing lots, tossing a coin, shuffling cards, and throwing dice were adequate if an independent person not otherwise involved in the study performed them.

• Unclear risk of bias: the study authors did not report the sequence generation method.

• High risk of bias: the sequence generation method was not random.

Allocation concealment

• Low risk of bias: participants and investigators enrolling participants could not foresee assignment because one of the following, or an equivalent method, was used to conceal allocation: central allocation, sequentially numbered drug containers of identical appearance; sequentially numbered, opaque, sealed envelopes.

• Unclear risk of bias: insufficient information available to permit a judgement of ‘low risk’ or ‘high risk’.

• High risk of bias: participants or investigators enrolling participants could possibly foresee assignments and thus introduce selection bias.

In addition to these criteria, we considered the implications of baseline imbalances in prognostic factors affecting the trial outcomes, as these may lead to selection bias (Corbett 2014).

Blinding of participants and personnel

• Low risk of bias: either of the following: no blinding or incomplete blinding, but the review authors judge that the outcome is not likely to be influenced by lack of blinding; or blinding of participants and key study personnel ensured, and it is unlikely that the blinding could have been broken.

• Unclear risk of bias: any of the following: insufficient information available to permit a judgement of ‘low risk’ or ‘high risk’; or the trial did not address this outcome.

• High risk of bias: either of the following: no blinding or incomplete blinding, and the outcome is likely to be influenced by lack of blinding; or blinding of key study participants and personnel attempted, but likely that the blinding could have been broken, and the outcome is likely to be influenced by lack of blinding.

Blinded outcome assessment

We considered blinding separately for different outcomes, as appropriate, and, to aid in the process, divided the domain into two categories: subjective and objective assessment.

• Low risk of bias: either of the following: no blinding of outcome assessment, but the review authors judge that the outcome measurement is not likely to be influenced by lack of blinding; or blinding of outcome assessment ensured, and it is unlikely that the blinding could have been broken.

• Unclear risk of bias: any of the following: insufficient information available to permit a judgement of ‘low risk’ or ‘high risk’; or the trial did not address this outcome.

• High risk of bias: either of the following: no blinding of outcome assessment, and the outcome measurement is likely to be influenced by lack of blinding; or blinding of outcome assessment, but likely that the blinding could have been broken, and the outcome measurement is likely to be influenced by lack of blinding.

Incomplete outcome data

• Low risk of bias: missing data were unlikely to make treatment effects depart from plausible values. The study used sufficient methods, such as multiple imputation, to handle missing data.

• Unclear risk of bias: there was insufficient information available to assess whether missing data in combination with the method used to handle missing data were likely to induce bias to the results.

• High risk of bias: the results were likely to be biased due to missing data.

Selective outcome reporting

• Low risk: the trial reported the following predefined outcomes: if the original trial protocol was available, the outcomes reported by the trial were listed in that protocol; if the trial protocol was obtained from a trial registry, the outcomes reported by the trial should have been those enumerated in the original protocol if the trial protocol was registered before or at the time that the trial was begun.

• Unclear risk: the study authors did not report all predefined outcomes fully, or it is unclear whether the study authors recorded data on outcomes or not.

• High risk: the study authors did not report one or more predefined outcomes; if the trial protocol was registered after the trial was begun, we did not consider those outcomes to be reliable.

For‐profit bias

In order to assess the study source of funding, this domain was added in place of the ‘other bias’ domain.

• Low risk of bias: the trial appears to be free of industry sponsorship or other type of for‐profit support that may manipulate the trial design, conductance, or reporting of trial results.

• Unclear risk of bias: the trial may or may not be free of for‐profit bias as the trial does not provide any information about clinical trial support or sponsorship.

• High risk of bias: the trial is sponsored by industry or received other type of for‐profit support.

Enriched population

Because the clinical effect of botulinum toxin treatment is easily perceived, Bt non‐naive participants are likely to recognise the presence or absence of clinical effects, or frequent adverse events, or both, effectively revealing the respective allocation arm. It is also relevant that, by preferentially including responders to Bt or excluding non‐responders to Bt, there is an increased likelihood that these participants respond more favourably to Bt than a naive population would. We opted to subdivide this domain in two: preferential enrolment of known positive responders to Bt; and exclusion of known poor responders to Bt.

• Low risk of bias: at least 70% of trial participants were Bt‐naive; the trial did not exclude any particular forms of cervical dystonia.

• Unclear risk of bias: the trial did not make explicit the percentage of participants who were known responders to Bt.

• High risk of bias: arbitrarily defined as more than 30% of participants non‐naive to Bt; explicit exclusion of people with forms of cervical dystonia known to have a poor response to Bt, namely people with pure anterocollis and retrocollis.

Dichotomous data

We based analysis of these data on the number of events and the number of people assessed in the intervention and comparison groups. We used these to calculate the risk ratio (RR) and 95% confidence interval (CI).

Continuous data

We based analysis of these data on the mean, standard deviation (SD) and number of people assessed for both the intervention and comparison groups to calculate mean difference (MD) and 95% CI. Where the MD was reported without individual group data, we used this to report the study results. If more than one study measured the same outcome using different validated tools, we calculated the standardised mean difference (SMD), namely Hedges’ (adjusted) g (Hedges 1985), and 95% CI. For interpretation of effect sizes with SMDs, we used a rule of thumb to define a small effect (SMD = 0.2), a moderate effect (SMD = 0.5), or a large effect (SMD = 0.8) (Cohen 1988). If necessary for comparison, we dichotomised rating scales using each study author's own criteria for improvement or no improvement.

Time‐to‐event data

We planned to analyse these data based on log hazard ratios and standard errors obtained from results of Cox proportional hazards regression models. We had planned to use these in order to calculate a hazard ratio (HR) and 95% CI.

Meta‐analysis

We based the decision whether or not to meta‐analyse data on an assessment of whether the interventions in the included trials were similar enough in terms of participants, settings, intervention, comparison and outcome measures to ensure meaningful conclusions from a statistically pooled result. We conducted data synthesis using a random‐effects model.

We pooled effect measures by applying the Mantel‐Haenszel method for dichotomous outcomes, and applying the inverse‐variance or generic inverse‐variance method for continuous outcomes. In addition, we had planned to pool time‐to‐event data using the generic inverse‐variance method. We presented all results with 95% CI.

We calculated the number of participants needed to treat for an additional beneficial outcome (NNTB) and for an additional harmful outcome (NNTH) from meta‐analysis estimates, rather than treating data as if they came from a single trial, as the latter approach is more prone to bias, especially when there are significant imbalances between groups within one or more trials in the meta‐analysis (Altman 2002). However, caution is needed in the interpretation of these findings since they may be misleading because of variation in the event rates in each trial, differences in the outcomes considered, and differences in clinical setting (Smeeth 1999).

Where there were no data that could be combined into a meta‐analysis we undertook a narrative approach to result synthesis.

Trial sequential analysis

In order to explore whether the cumulative data were of adequate power to evaluate the primary outcomes of this review, we performed a trial sequential analysis (Wetterslev 2008), and calculated a required information size (also known as the heterogeneity‐adjusted required information size) (Wetterslev 2009). Trial sequential analysis aims to evaluate whether statistically significant results of meta‐analysis are reliable by accounting for the required information size (i.e. the number of participants in the meta‐analysis required to accept or reject an intervention effect). The technique is analogous to sequential monitoring boundaries in single trials. Trial sequential analysis adjusts the threshold of statistical significance and has been shown to reduce the risk of random errors due to repetitive testing of accumulating data (Imberger 2016).

We calculated the required information size and computed the trial sequential monitoring boundaries using the O’Brien‐Fleming approach (O'Brien 1979). The required information size was based on the event proportion or standard deviation in the control group; assumption of a plausible relative risk reduction (RRR) of 10%; a 5% risk of type I error; a 20% risk of type II error (power = 80%); and the observed heterogeneity of the meta‐analysis (Jakobsen 2014; Wetterslev 2009).

Assessing the quality of the evidence

As recommended by the Grading of Recommendations Assessment, Development and Evaluation (GRADE) Working Group methodology (Schünemann 2011), two reviewers independently assessed all of the outcomes in the following domains: study limitations, inconsistency, indirectness, imprecision and publication bias. In case of disagreement the authors attempted to reach consensus, consulting an independent third reviewer if necessary. For this purpose, we used the GRADEprofiler (GRADEpro GDT) software tool (GRADEpro GDT 2014), which we then used to export a 'Summary of findings' table for inclusion in the review manuscript.

To ensure the consistency and reproducibility of GRADE judgements, we applied the following criteria to each domain for all key comparisons of the critical outcomes.

• Study limitations: we downgraded once if more than 30% of participants were from studies classified as being at a high risk of bias across any domain, with the exception of 'for‐profit bias'.

• Inconsistency: we downgraded once if heterogeneity was statistically significant or if the I² value was more than 40%. When a meta‐analysis was not performed we downgraded once if trials did not show effects in the same direction.

• Indirectness: we downgraded once if more than 50% of the participants were outside the target group.

• Imprecision: we downgraded once if the optimal information size criterion was not met or, alternatively, if it was met but the 95% CI fails to exclude important benefit or important harm (Guyatt 2011).

• Publication bias: we downgraded once where there was direct evidence of publication bias or if estimates of effect based on small scale, industry‐sponsored studies raised a high index of suspicion of publication bias.

We applied the following definitions to the quality of evidence (Balshem 2011):

• high quality: we are very confident that the true effect lies close to that of the estimate of the effect;

• moderate quality: we are moderately confident in the effect estimate; the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different;

• low quality: our confidence in the effect estimate is limited; the true effect may be substantially different from the estimate of the effect;

• very low quality: we have very little confidence in the effect estimate; the true effect is likely to be substantially different from the estimate of effect.

'Summary of findings' table

As has become standard practice in Cochrane Reviews, we have included a 'Summary of findings' table to present the main findings of this review in a simple tabular format, based on the results of the GRADE analysis. In particular, we included key information concerning the quality of evidence, the magnitude of effect of the interventions examined, and the sum of available data on the outcome overall cervical dystonia improvement, proportion of participants with adverse events, subjective change as assessed by the patient, cervical dystonia associated pain, sore throat/dry mouth, and dysphagia (difficulty swallowing).