Types of studies

Randomised controlled trials (RCTs), blinded, single, or multiple dose, parallel‐designed, of any duration, assessing the efficacy or safety, or both, of botulinum toxin type A (BtA) treatment versus placebo, in people with blepharospasm, were eligible for inclusion in this review. We excluded non‐parallel study designs, namely cross‐over trials, due to uncertainty about whether this type of study design was appropriate to study people with blepharospasm, as well as methodological concerns with regards to detection and performance bias.

There were no restrictions regarding the number of participants recruited to trials, or the number of recruitment centres.

Types of participants

Adults (i.e. 18 years of age or older), in any setting, with a clinical diagnosis of blepharospasm, made by a physician, specialist, or other healthcare provider. We included trials enrolling participants with any form of blepharospasm, with or without widespread dystonias. We included participants with prior exposure to botulinum toxin, or those taking concomitant medications, if they were on stable regimens.

Types of interventions

Intramuscular injections of botulinum toxin type A (BtA) compared to placebo. We allowed all administration schedules and injection techniques.

Types of outcome measures

Electronic searches

We ran the final search for the original version of this review in June 2003, based on the search strategy developed for Cochrane Movement Disorders to identify all papers since 1977, the first year that botulinum toxin was used therapeutically in any condition. We ran the search for the current update for the last time in July 2020.

For the identification of studies considered for inclusion in this review, we developed detailed search strategies for each database searched. Please see Appendix 1 for the Cochrane Central Register of Controlled Trials (CENTRAL) strategy, Appendix 2 for the MEDLINE search strategy, and Appendix 3 for the Embase strategy.

We assessed non‐English language papers, translated them as necessary, and evaluated them for inclusion.

We did not search trials registries.

Searching other resources

The search strategy also included:

• searches of reference lists of located trials and review articles concerning botulinum toxin;

• handsearch of abstracts of international congresses relevant to the fields of movement disorders and botulinum toxins (American Academy of Neurology, Movement Disorders Society, International Association of Parkinsonism and Related Disorders, and International Neurotoxin Association (1985 to July 2020));

• personal communication with other researchers in the field;

• contact with drug manufacturers;

• whenever necessary, we contacted authors of published trials for further information and unpublished data.

Selection of studies

Two review authors independently screened all titles and abstracts identified from searches to determine which ones met the inclusion criteria. We retrieved in full text any papers identified as potentially relevant by at least one review author, or those without an available abstract. Two review authors independently screened full‐text articles, with discrepancies resolved by discussion, and by consulting a third review author, where necessary, to reach consensus. We collated duplicate publications and presented our references by individual study. We outlined the screening and selection process in a PRISMA flow chart (Liberati 2009); see Figure 1.

Figure 1

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Flow diagram for study selection

Data extraction and management

Two review authors independently extracted data from included studies, using a piloted data extraction form. We resolved any discrepancies by discussion, until consensus was reached, or through consultation with a third review author, where necessary. Data extracted included the following items from each study.

• Participants: inclusion and exclusion criteria, demographics and clinical baseline characteristics, number and reasons for dropping out, exclusions, and loss to follow‐up, if any

• Interventions: full description of intervention, duration of treatment period and follow‐up, providers, and co‐interventions, if any

• Comparisons: number of randomised participants to each arm, compliance and number of dropouts, reasons for dropping out, and ability to perform an intention‐to‐treat analysis

• Outcomes: definition of outcomes, use of validated measurement tools, time point measurements, change from baseline or post‐interventional measures, and missing outcomes, if any

• Study design: interventional, randomised, controlled, double‐blind.

Assessment of risk of bias in included studies

We assessed the risk of bias of included studies according to the domains described in the Cochrane tool for assessing risk of bias, and classified the risk of bias for each domain as high, unclear, or low, and the overall assessment as high or low (Higgins 2011a). We assessed two further domains, which are described below: enriched population and independent funding. We used the following definitions for each domain in the 'Risk of bias' assessment.

• Random sequence generation (checking for possible selection bias). We assessed 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); high risk of bias (non‐random process used, e.g. allocation by birth year or by judgement).

• Allocation concealment (checking for possible selection bias). We assessed the method used to conceal allocation to interventions prior to assignment, to determine whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment. We assessed 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); high risk of bias (e.g. open list).

• Blinding of participants and personnel (checking for possible performance bias). We assessed the methods used to blind study participants and personnel from knowledge of which intervention a participant received. We assessed methods as: low risk of bias (study stated that it was blinded and described 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 stated that it was blinded but did not provide an adequate description of how it was achieved). Studies that were not double‐blind were considered to have high risk of bias.

• Blinding of outcome assessment (checking for possible detection bias). We assessed the methods used to blind outcome assessors from knowledge of which intervention a participant received. We assessed the methods as: low risk of bias (study had a clear statement that outcome assessors were unaware of treatment allocation, and ideally described how this was achieved); unclear risk of bias (study stated that outcome assessors were blind to treatment allocation but lacked a clear statement on how it was achieved). We considered studies where outcome assessment was not blinded as having a high risk of bias.

• Selective reporting (checking for reporting bias). We assessed whether primary and secondary outcome measures were pre‐specified, and whether these were consistent with those reported. We assessed selective reporting as: low risk of bias (studies reporting results for primary and secondary outcomes); unclear risk of bias (study reporting insufficient information to permit judgement); high risk of bias (not all pre‐specified outcomes reported, or 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 assessed the methods used to deal with incomplete data as: low risk (< 10% of participants did not complete the study, trial authors used ‘baseline observation carried forward’ analysis, or both); unclear risk of bias (used 'last observation carried forward' analysis); high risk of bias (used 'completer' analysis).

In addition to these criteria, we also added two more items for consideration.

• Enriched population. Because the clinical effect of botulinum toxin treatment is easily perceived, participants not naive to botulinum toxin are likely to recognise the presence or absence of beneficial clinical effects, or frequent adverse events, or both, effectively revealing the respective allocation arm. It is also relevant that by preferentially including responders to botulinum toxin or excluding non‐responders to botulinum toxin, there is an increased likelihood that these participants would respond more favourably to botulinum toxin than a naive population would. We opted to subdivide this domain in two: preferential enrolment of known positive responders to botulinum toxin; and exclusion of known poor responders to botulinum toxin.

  • Low risk of bias: at least 70% of trial participants were naive to treatment with botulinum toxin; the trial did not exclude any particular form of blepharospasm.

  • Unclear risk of bias: the trial did not make explicit the percentage of participants who were known to be naive to botulinum toxin.

  • High risk of bias: arbitrarily defined as more than 30% of participants who were not naive to botulinum toxin; explicit exclusion of people with forms of blepharospasm associated with a poorer response to botulinum toxin.

• For‐profit bias. In order to assess the study source of funding, we added this domain

  • Low risk of bias: the trial appeared to be free of industry sponsorship or other types of for‐profit support that may introduce bias into trial design, conduct, or trial results.

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

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

Measures of treatment effect

We compared disorder‐related symptoms at baseline to symptoms in weeks four to six post‐injection in the BtA and placebo arms. We extracted continuous outcomes whenever possible, pooled the data from the studies, where adequate, and used them for comparison.

Unit of analysis issues

Whenever the included studies had multiple arms with different doses of botulinum toxin, we combined all groups to create a single pair‐wise comparison, using the Review Manager 5 calculator, according to the methods suggested by Cochrane (Higgins 2011b; Review Manager 2014). We also would have opted to create a single, pair‐wise comparison in cases when multiple treatment groups, using different interventions (e.g. onabotulinumtoxinA and abobotulinumtoxinA), were compared to the same comparator.

This method combines all relevant experimental intervention groups of the study into a single group, and all relevant control intervention groups into a single control group. This approach avoids the duplication of the control group, which would happen if multiple comparisons (e.g. BtA dose 1 versus placebo; BtA dose 2 versus placebo) were included in the meta‐analysis, as well as the loss of information if one dose group is chosen over the others. If applicable, we plan to explore the effect of dose in subgroup analysis.

For dichotomous outcomes, we planned to sum both the sample sizes and the numbers of people with events across groups. For continuous outcomes, we planned to pool means and standard deviations in a meta‐analysis (Higgins 2011b; Higgins 2011c).

Dealing with missing data

For missing outcome or summary data, we used imputation methods to derive the missing data (where possible), and reported any assumptions in the review. In these cases, we carried out sensitivity analyses to investigate the effects of any imputed data on pooled effect estimates.

As the first option, we used the available information (e.g. standard error (SE), 95% CI, or exact P value) to recover the missing data algebraically (Higgins 2011b; Higgins 2011c; Wiebe 2006). When change from baseline SD data were not reported, or we were unable to extract them, we attempted to create a correlation coefficient, based on another study in the review, and then used this correlation coefficient to impute a change from baseline SD (Abrams 2005; Follmann 1992; Higgins 2011b).

If this failed, and there was at least one sufficiently large and similar study, we planned to use a method of single imputation (Furukawa 2006; Higgins 2011b).

Lastly, if there were a sufficient number of included studies with complete information, we planed to use multiple imputation methods to derive missing data (Carpenter 2013; Rubin 1991).

If none of these methods proved successful, we planned to conduct a narrative synthesis for the data in question.

Assessment of heterogeneity

We assessed whether studies were similar enough to allow pooling of data using meta‐analysis. Where data were pooled using meta‐analysis, we assessed the degree of heterogeneity by visual inspection of forest plots and by examining the Chi² test for heterogeneity (Deeks 2011). We quantified heterogeneity using I² (Higgins 2003). We considered an I² value of 50% or more to represent substantial levels of heterogeneity, but interpreted this value in light of the size and direction of effects, and the strength of the evidence for heterogeneity, based on the P value from the Chi² test.

Assessment of reporting biases

We included too few studies in this review, i.e. fewer than 10, to allow construction of a funnel plot (Sterne 2001), and formal testing of asymmetry, which may indicate publication bias (Peters 2006). Should enough studies be included in future updates of this review, we plan to undertake these analyses.

Data synthesis

We performed the analyses with Review Manager 5 (Review Manager 2014), Stata version 15 (Stata), and Trial Sequential Analysis (TSA; (Thorlund 2011; TSA 2011)).

Subgroup analysis and investigation of heterogeneity

We planned subgroup analyses for the following areas, independently of the presence of significant heterogeneity.

• Different BtA formulations

• Different BtA doses, all defined arbitrarily: high (Botox or Xeomin > 200 U; Dysport = 1000 U), medium (Botox or Xeomin 100 U to 200 U; Dysport = 500 U), and low (Botox or Xeomin < 100 U; Dysport = 250 U

Sensitivity analysis

We conducted sensitivity analyses for every study for which we applied imputation methods.