苯海索治疗脑瘫肌张力障碍
摘要
研究背景
每1000名活产婴儿中多达2.1人患有脑瘫，包括一系列运动问题和运动障碍。脑瘫患者中一种常见的运动障碍是肌张力障碍：持续或间歇性的不自主肌肉痉挛和收缩导致扭曲、重复运动和异常姿势。不自主的收缩通常是非常痛苦和苦恼的，并对活动和参与造成重大限制。
口服药物通常是治疗肌张力障碍的一线药物。苯海索是临床医生经常用于治疗脑瘫患者肌张力障碍的一种药物。
研究目的
根据世界卫生组织（World Health Organization, WHO）的国际功能残疾健康分类（nternational Classification of Functioning, ICF）领域的损伤、活动和参与，评价苯海索对肌张力障碍性脑瘫患者的影响。我们还评价了服用该药物的人的不良反应类型和发生率。
检索策略
我们于2017年5月检索了CENTRAL、MEDLINE、Embase、其他八个数据库和两个试验注册库，并检索了参考文献列表和引文以找到更多研究。
纳入排除标准
我们纳入了比较口服苯海索与安慰剂治疗脑瘫肌张力障碍的随机对照试验。我们纳入了针对任何年龄的肌张力障碍性脑瘫的儿童和成人的研究，无论是孤立的还是伴有痉挛、共济失调、舞蹈症、手足徐动症和/或肌张力减退等相关运动障碍的患者。无论研究作者是否在其研究人群中指定用于诊断肌张力障碍的方法，我们都将其纳入了。主要结局是肌张力障碍和不良反应的变化。次要结局是：活动，包括活动能力和上肢功能；参与日常生活活动；痛；和生活质量。
资料收集与分析
我们使用了Cochrane推荐的标准方法学程序。
主要结果
我们确定了一项在澳大利亚开展的符合纳入标准的研究。这是一项随机、双盲、安慰剂对照、交叉试验，受试者为16名儿童（10名男孩和6名女孩），主要患有肌张力障碍性脑瘫，平均年龄为9岁（标准差为4.3岁，范围2至17岁）。我们认为该试验在选择、实施、检测、损耗、报告和其他偏倚来源的风险较低。我们将证据的GRADE质量评为低质量。
我们发现，按照Barry Albright肌张力障碍量表（Barry Albright Dystonia Scale, BADS）测量的肌张力障碍变化的平均随访分数没有差异，该量表以5分制量表评价八个身体区域的肌张力障碍（0=0至4=严重），结果总分为0到32分。治疗组的BADS评分高2.67分（95%置信区间（confidence interval, CI） [‐2.55, 7.90]；低质量证据），即更严重的肌张力障碍。苯海索可能与不良反应风险增加有关（风险比=2.54，95%CI [1.38, 4.67]；低质量证据）。
上肢功能质量测试的上肢功能平均随访分数没有差异，该测试有四个领域，共同评价36个项目（每个项目得分1或2），总得分为0到100。与对照组相比，治疗组的评分低4.62分（95%CI [‐10.98, 20.22]；低质量证据），对应的功能更差。我们发现低质量证据表明治疗组在日常生活活动中的参与度有所提高（以更高的分数表示），通过三个工具衡量：目标实现量表（最多五个功能目标在5分制量表上得分（‐2=远低于预期至+2=远高于预期））高18.86分（95%CI [5.68, 32.03]），加拿大职业绩效测量（COPM）的满意度分量表（COPM；对最多五个问题领域的绩效的满意度以10分制评分（1=完全不满意至10=非常满意） ）高2.91分（95%CI [1.01, 4.82]）；而COPM的绩效分量表（在多达5个问题领域的绩效以10分制评分（1=不能做到；10=能够做到非常好））高2.24分。
该研究没有报告关于疼痛或生活质量的数据。
作者结论
目前，关于苯海索治疗脑瘫患者的以下结局的有效性的证据不足：肌张力障碍的变化、不良反应、上肢功能的增加和日常生活活动参与度的提高。该研究没有评价疼痛或生活质量。需要进行更大规模的随机、对照、多中心试验，这些试验还检查对疼痛和生活质量的影响，以确定苯海索治疗脑瘫患者的有效性。
PICO
简语概要
苯海索治疗脑瘫肌张力障碍
系统综述问题
苯海索对患有称为肌张力障碍的运动问题的脑瘫患者来说是一种有效的治疗方法吗？
系统综述背景
脑瘫是一种常见的疾病，涵盖了一系列运动问题。一种常见的运动问题是肌张力障碍，这使得脑瘫患者难以控制自己的运动。他们有无法控制的、不想要的——通常是痛苦和苦恼的——肌肉收缩。这种收缩会降低人们移动、进行自我照护活动、说话和参与日常活动的能力。
医生经常使用药物来治疗这种困难的情况，包括苯海索。然而，对脑瘫和肌张力障碍患者开具苯海索的所有益处和危害仍然未知。
研究特征
2017年5月，我们检索了所有研究苯海索对肌张力障碍性脑瘫患者有效性的临床试验。我们纳入了一项澳大利亚的试验，该试验纳入了16名患有脑瘫和肌张力障碍的儿童（10名男孩，6名女孩）。他们的平均年龄为九岁。
孩子们被分成两个不同的组。两组都服用了12周的苯海索和12周的安慰剂（看起来与苯海索相同但没有活性成分的东西），中间有4周的中断时间，在此期间他们都没有服用药物。两组之间的唯一区别是，一组从苯海索开始，然后服用安慰剂，而另一组从安慰剂开始，然后服用苯海索。
主要研究结果
我们没有发现任何证据表明苯海索可有效减轻脑瘫和肌张力障碍儿童的肌张力障碍或改善上臂功能。苯海索可能与副作用风险增加有关（躁动、便秘、口干和睡眠不佳）。有一些证据表明，苯海索可能会改善儿童和家庭围绕改善对日常生活活动的参与度而设定的个人目标。该研究没有评价疼痛或生活质量。
证据质量
我们将证据质量评为低质量，因为一项研究纳入的儿童数量少，并且没有其他研究支持该发现。因此，我们不确定苯海索在减轻肌张力障碍或改善手臂功能和参与脑瘫和肌张力障碍患者日常活动方面的有效性。
Authors' conclusions
Summary of findings
| Trihexyphenidyl compared with placebo for dystonia in cerebral palsy | |||||
| Patient or population: children with dystonic cerebral palsy Settings: one tertiary care hospital Intervention: trihexyphenidyl Comparison: placebo | |||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | Number of participants | Quality of the evidence | |
| Assumed risk | Corresponding risk | ||||
| Placebo | Trihexyphenidyl | ||||
| Change in dystonia from baseline Measured by: BADS (eight body regions assessed for dystonia on a five‐point scale (0 = none to 4 = severe), minimum score 0 to maximum score 32; higher score = greater severity of dystonia) Follow‐up: 12 weeks | The mean follow‐up score in the control group was 15.50 points | The mean follow‐up score in the intervention group was 2.67 points higher (2.55 lower to 7.90 higher) | — | 16 | ⊕⊕⊝⊝ Lowa |
| Adverse effectsb (mood disturbance, irritability, behavioural change, constipation) Measured by: counts of number and type Follow‐up: various (includes data assessed at both 12 and 28 weeks) | 375 per 1000 | 1000 per 1000 | RR 2.54 (1.38 to 4.67) | 16 | ⊕⊕⊝⊝ |
| Participation in activities of daily living:individual goal setting Measured by: GAS (up to 5 functional goals scored on a 5‐point scale (−2 = much less than expected to +2 = much more than expected); higher score = better than expected outcome) Follow‐up: 12 weeks | The mean follow‐up score in the control group was 27.63 points | The mean follow‐up score in the intervention group was 18.86 points higher (5.68 higher to 32.03 higher) | — | 16 | ⊕⊕⊝⊝ |
| Participation in activities of daily living:satisfaction with individual goals Measured by: satisfaction subscale of the COPM (satisfaction with performance in up to 5 problem areas scored on a 10‐point scale (1 = not satisfied at all to 10 = extremely satisfied); higher score = greater satisfaction) Follow‐up: 12 weeks | The mean follow‐up score in the control group was 2.96 points | The mean follow‐up score in the intervention group was 2.91 points higher (1.01 higher to 4.82 higher) | — | 16 | ⊕⊕⊝⊝ |
| Participation in activities of daily living:performance of individual goals Measured by: performance subscale of the COPM (up to five problem areas scored on a 10‐point scale (1 = not able to do to 10 = able to do extremely well; higher score = better performance) Follow‐up: 12 weeks | The mean follow‐up score in the control group was 3.14 points | The mean follow‐up score in the intervention group was2.24 points higher (0.64 higher to 3.84 higher) | — | 16 | ⊕⊕⊝⊝ |
| Quality of life | Not measured | ||||
| *The basis for the assumed risk is provided in the footnotes. The corresponding risk (and its 95% CI) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI) | |||||
| GRADE Working Group grades of evidence | |||||
| aDowngraded two levels due to imprecision; small sample size from one study only. | |||||
Background
Description of the condition
Cerebral palsy has been described as "a group of permanent disorders of the development of movement and posture, causing activity limitation ... [attributable] to non‐progressive disturbances that occurred in the developing fetal or infant brain" (Rosenbaum 2007). Disturbances of sensation, perception, cognition, communication and behaviour, epilepsy and secondary musculoskeletal problems often accompany the motor disorders of cerebral palsy.
Cerebral palsy is a common childhood condition, occurring in approximately 2.11 of every 1000 live births (Oskoui 2013). It encompasses motor problems such as spasticity (increased muscle tone); hyperkinetic disorders, such as dystonia and choreoathetosis where there is unwanted excessive movement; and, less commonly, ataxia (uncoordinated movement). However, many children present with a mixed movement disorder.
Dystonia frequently occurs in children with cerebral palsy and is "characterised by involuntary sustained or intermittent muscle contractions that cause twisting and repetitive movements, abnormal postures, or both” (Sanger 2003). Of the methods used to diagnose dystonia, the one with the greatest credibility is the Hypertonia Assessment Tool (HAT; Jethwa 2010). The HAT is a seven‐item, standardised clinical assessment tool for children over four years of age, which is used to reliably differentiate the various types of paediatric hypertonia, namely spasticity, dystonia and rigidity (Jethwa 2010). Dystonia can result from an abnormality in the basal‐ganglia cortical pathway and can be measured clinically using a variety of scales. It may affect one or more limbs, or be present throughout the child’s whole body, including the mouth, eyes and neck. The involuntary contractions are often very painful and distressing. Dystonia can reduce activity and participation across many of the health‐related domains described in the World Health Organization's (WHO) International Classification of Functioning, Disability and Health (ICF) model (WHO ICF 2003).
The percentage of children with cerebral palsy identified as having dominant dyskinetic cerebral palsy (including dystonia and choreoathetosis) is substantial, ranging from 6% in Australia to 15% in Europe (ACPR 2016; Bax 2006; Himmelmann 2007). Children who are accurately identified as spasticity‐dominant can also have dyskinesia, which can add to their disability and discomfort. Traditionally, identifying dystonia and differentiating it from spasticity relied primarily on clinical examination and observation, with uncertain reliability and validity. The accurate identification of dyskinesia in children with cerebral palsy has been facilitated by the development of the HAT, which reliably differentiates the subtypes of hypertonia (Jethwa 2010).
Dystonia can have devastating effects on function, including impairment of communication and swallowing, and it can create difficulties in completing self‐care tasks and being comfortably seated in a wheelchair. Children also get into cycles of dystonia causing musculoskeletal pain, which in turn exacerbates their dystonia. The worst example of this is the dystonic crisis, which can require muscle paralysis/sedation (Allen 2014). These difficulties can negatively affect the quality of life of the individual and their caregivers.
Description of the intervention
Dystonia is a difficult movement disorder with limited management options available for treatment. Oral medications are often the first‐line of treatment for this challenging condition.
Trihexyphenidyl (also known as benzhexol) is a selective muscarinic acetylcholine receptor antagonist, blocking cholinergic activity centrally and peripherally (NIH 2005). It is also thought to increase the availability of dopamine, a brain chemical that is critical in the initiation and smooth control of voluntary muscle movement. Trihexyphenidyl is available in liquid form, as a tablet, or as an extended‐release (long‐acting) capsule. The onset of action of this medication occurs within an hour of oral administration. It has a peak effect 2 to 3 hours after administration, and the duration of action can last from 6 to 12 hours.
How the intervention might work
The pathophysiology of dystonia involves a dysfunction in the basal ganglia. The pathways between the basal ganglia and the cortex are influenced by neurotransmitters that act on various receptors in feedback loops causing positive or negative effects. The mechanism of action of trihexyphenidyl in reducing dystonia is believed to be in the basal ganglia where it reduces acetylcholine and increases dopamine (Carranza del Rio 2011). By treating dystonia and its associated impairments, clinicians hope to improve activity and decrease associated pain and discomfort.
Why it is important to do this review
Medication is frequently used for dystonia but little information is available as to whether it is effective, and side effects are common. Most of the published studies assessing medications are small and descriptive, limiting the ability to draw conclusions on its effects. Prospective case series, such as Sanger 2007, along with a few retrospective case series, like Ben‐Pazi 2011, and Hoon 2001, have reported inconsistent results for trihexyphenidyl in cerebral palsy; however, there is a need to examine evidence from existing randomised trials. This review will bring together and evaluate existing trials to clarify the benefits and risks of trihexyphenidyl for dystonia in cerebral palsy.
Objectives
To assess the effects of trihexyphenidyl in people with dystonic cerebral palsy, according to the World Health Organization's (WHO) International Classification of Functioning, Disability and Health (ICF) domains of impairment, activity and participation. We also assessed the type and incidence of adverse effects in people taking the drug.
Methods
Criteria for considering studies for this review
Types of studies
Randomised controlled trials (RCTs).
Types of participants
Children and adults with dystonic cerebral palsy, either in isolation or with the associated movement disorders of spasticity, ataxia, chorea, athetosis and/or hypotonia were eligible. Although we applied no age restrictions, we found no studies reporting outcomes for adults.
We included studies regardless of whether or not the study authors specified the method used to diagnose dystonia in their study population. We did this in order to include all studies with relevant findings. We do concede, however, that studies using the HAT may have greater credibility than those using other or unspecific methods of diagnosis (Jethwa 2010).
Types of interventions
Oral trihexyphenidyl, regardless of dosage or frequency of administration, used to treat dystonia in cerebral palsy.
The control group had to be a placebo group. Trials with more than one comparison group were eligible, as long as one group received trihexyphenidyl and one group received placebo.
Types of outcome measures
Primary outcomes
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*Change in dystonia from baseline, as assessed using the Barry‐Albright Dystonia scale (Barry 1999), Dyskinesia Impairment Scale (Monbaliu 2012), or electrophysiological measures of dystonia
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*Adverse effects (mood disturbance, irritability, behavioural change, constipation)
Secondary outcomes
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Activity, including mobility and upper limb function, as measured by validated scales such as the Canadian Occupational Performance Measure (Law 2005), Global Assessment Scale (Endicott 1976), Quality of Upper Extremity Skills Test (QUEST 1992), Melbourne Assessment of Unilateral Upper Limb Function (Randall 1999), Gross Motor Function Measure (Hanna 2008), Three Dimensional Gait Analysis (Ferber 2016), Timed Up and Go Test (TUG 2005), Functional Independence Measure (WeeFIM 1994), and High‐level Mobility Assessment Tool (Williams 2006)
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*Participation in activities of daily living at home, school, in the community and in the workforce, as measured by validated scales such as the Children's Assessment of Participation and Enjoyment (King 2004), the Canadian Occupational Performance Measure (Law 2005), and the Global Assessment Scale (Endicott 1976)
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Pain, as measured by validated scales such as the Wong‐Baker FACES Pain Rating Scale (Wong‐Baker FACES Pain Rating Scale 2001)
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*Quality of life, as measured by validated scales such as the Pediatric Quality of Life Inventory (PedsQL 1999), the Caregiver Priorities and Child Health Index of Life with Disabilities (Narayanan 2007), or other validated scale
We placed no restrictions on length of outcome follow‐up.
We used those outcomes marked with an asterisk (*) to populate the 'Summary of findings' table.
Search methods for identification of studies
This review is based on a published protocol (Baker 2017).
Electronic searches
We searched the electronic databases and trials registers listed below up to May 2017.
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Cochrane Register of Studies Online, which includes the Cochrane Developmental, Psychosocial and Learning Problems Group Specialised Register (crso.cochrane.org; searched 25 May 2017).
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MEDLINE Ovid (1946 to May week 3 2017).
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MEDLINE In‐Process & Other Non‐Indexed Citations Ovid (searched 25 May 2017).
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MEDLINE Epub Ahead of Print Ovid (searched 25 May 2017).
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Embase Ovid (1974 to 2017 week 21).
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CINAHL EBSCOhost (Cumulative Index to Nursing and Allied Health Literature; 1937 to 25 May 2017).
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Science Citation Index Web of Science (SCI; 1990 to 24 May 2017).
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Conference Proceedings Citation Index – Science Web of Science (CPCI‐S; 1990 to 24 May 2017).
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Cochrane Database of Systematic Reviews (CDSR; 2017, Issue 5) part of the Cochrane Library (searched 26 May 2017).
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Database of Abstracts of Reviews of Effects (DARE; 2015, Issue 2. Final Issue) part of the Cochrane Library (searched 26 May 2017).
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LILACS (lilacs.bvsalud.org/en; searched 26 May 2017).
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ClinicalTrials.gov (clinicaltrials.gov; searched 26 May 2017).
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WHO International Clinical Trials Registry Platform (ICTRP) (who.int/ictrp/en; searched 26 May 2017).
We developed a search strategy in MEDLINE, which we adapted for each of the sources listed above (Appendix 1) . We did not apply any date or language restrictions.
Searching other resources
We checked the reference lists of included reports and relevant reviews. In addition, we contacted experts to identify any additional studies not retrieved by our electronic searches.
Data collection and analysis
We were not able to use many of our planned methods because only one study met the criteria for inclusion in the review (Criteria for considering studies for this review). Details of unused methods can be found in Baker 2017 and Table 1. What follows next is a description of methods that we did use.
| Method | Unused methods |
| Measures of treatment effect | Continuous data For continuous outcomes we will calculate the MD and corresponding 95% CI if studies use the same rating scales. We will calculate the SMD with 95% CIs if studies use different scales to measure the same outcomes. As recommended in section 9.4.5.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017), we will focus on final values unless some of the studies use change scores. We will combine studies that report final values with studies that report only change scores in the same meta‐analysis, provided that the studies use the same rating scale. We will conduct the analysis according to age, as children and adults respond differently to medication. We will combine the data from all groups in studies that have trihexyphenidyl in more than one group (i.e. different frequencies) and then separate these when performing the subgroup analysis to see how the different frequencies influence the results (see item four in the Subgroup analysis and investigation of heterogeneity section). |
| Multiple outcomes If studies provide multiple, interchangeable measures of the same construct at the same point in time, we will calculate the average SMD across the outcomes and the average estimated variances, as recommended in section 16.1.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). | |
| Unit of analysis issues | Cluster‐RCTs If included trials use cluster randomisation, we will extract an ICC and use this to reanalyse the data. Where no ICC is given and a unit of analysis error appears to exist, we will contact the trial authors and ask them to provide either an ICC or the raw data to enable calculation of an ICC. Where no ICC is made available, we will search for similar studies from which we can impute an ICC, or seek statistical advice to obtain an estimate of the ICC. |
| Dealing with missing data | We will contact trial investigators to request missing data. If the trialists provide missing data, we will conduct a meta‐analysis according to intention‐to‐treat principles using all data and keeping participants in the treatment group to which they were originally randomised, regardless of the treatment they actually received, as recommended in section 16.1.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). If missing data are not provided, we will analyse only the available data. If there is concern regarding a high level of missing data, such that data could not be included in a meta‐analysis, we will include a qualitative summary in the text of the review. We will document missing data and attrition in the 'Risk of bias' tables, and we will explore how missing data might affect the interpretation of the results by conducting a sensitivity analysis. |
| Assessment of heterogeneity | We will assess clinical heterogeneity by comparing the between‐trials distribution of participant characteristics (e.g. children versus adults) and intervention characteristics (e.g. treatment type and dose), and assess methodological heterogeneity by comparing trial characteristics (e.g. cross‐over versus parallel design). We will evaluate statistical heterogeneity using the I2 statistic and the Chi2 test of heterogeneity, with statistical significance set at P value < 0.10. As recommended in section 9.5.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017), we will consider I2 values as follows.
We will report Tau2 as an estimate of the between‐study variance when reporting the results from the random‐effects model. |
| Assessment of reporting biases | If we identify 10 or more studies, we will use funnel plots to investigate the relationship between intervention effect and study size. We will explore possible reasons for any asymmetry found. We will analyse the funnel plot of the data to ascertain asymmetry. Asymmetry of a funnel plot may indicate, among other things, publication bias or poor methodological quality (Egger 1997). |
| Data synthesis | We will synthesise results in a meta‐analysis using a fixed‐effect model when studies are similar enough with regard to the intervention, population and methods, to assume that the same treatment effect is estimated. We will synthesise results in a meta‐analysis using a random‐effects model when statistical heterogeneity is found or when studies differ enough with regard to the intervention, population, and methods, to assume that different yet related treatment effects are estimated, and when it is deemed to be clinically relevant, as recommended in section 9.4.3.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017). |
| Subgroup analysis and investigation of heterogeneity | We will conduct the subgroup analyses listed below.
We will also look at the number of participants per study to determine if this is sufficient to perform a subgroup analysis. |
| Sensitivity analysis | We will conduct sensitivity analyses to investigate the effect on the overall results of excluding trials that meet the criteria described below.
We will also conduct a sensitivity analysis for studies with very low risk of bias. In addition, we will conduct a sensitivity analysis using a range of ICCs to assess the impact on treatment effect. |
CI: confidence intervals; ICC: intraclass correlation coefficient; MD: mean difference; SMD: standardised mean difference.
Selection of studies
Two review authors, ARH and AS, independently screened the titles and abstracts of the citations identified from the search, discarding those that were clearly irrelevant. They then obtained the full texts of those studies that met, or seemed to meet, the inclusion criteria (Criteria for considering studies for this review), and they assessed them for relevance. KW acted as arbiter in the event of dispute. We recorded our decisions in a PRISMA flow diagram (Moher 2009).
Data extraction and management
Two review authors (ARH and AS) independently extracted data from the included study using a data extraction form designed and piloted for this review. They extracted the following information.
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Study methods and setting: study type (type of RCT), study site, country of publication, language of publication, publication type and study duration.
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Participant details: age, sex, diagnosis and diagnosis tool.
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Intervention details: intervention type, including dosage, mode of delivery, frequency and duration; placebo type, including dosage, mode of delivery, frequency and duration.
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Outcomes: all primary and secondary outcomes (see Types of outcome measures).
We resolved disagreements through consultation with KW.
ARH entered data into Review Manager 5 (RevMan 5), which KW checked for accuracy (RevMan 2014).
Assessment of risk of bias in included studies
Two review authors (ARH and AS) independently assessed the risk of bias in the included study using the tool described in section 8.5.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017). For the study, they judged the risk of bias to be either low, high or unclear, for each of the seven domains described in Appendix 2. They resolved disagreements by discussion with KW.
Measures of treatment effect
Dichotomous data
We had planned to analyse dichotomous outcomes by calculating the odds ratio (OR) and corresponding 95% confidence intervals (CI). However, because adverse effects (the only dichotomous outcome in this review) were frequent in the one included study, we calculated the risk ratio (RR) and corresponding 95% CI to provide a more interpretable statistic.
Continuous data
As recommended in section 9.4.5.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017), we performed an ANCOVA to estimate the change score due to the one included study using change scores. A potential problem of including change scores is that the standard deviation of changes may not be reported in the original study (Higgins 2011a).
See also Baker 2017 and Table 1.
Unit of analysis issues
The included study was a cross‐over trial, and we used the data from the first period of the cross‐over. We did not include any cluster‐randomised trials (see Baker 2017; Table 1).
Dealing with missing data
We assessed missing data and dropouts for the included study. We reported the number of participants included in the final analysis as a proportion of all participants in the study, reporting reasons for missing data (dropouts) according to their randomised groups (trihexyphenidyl and placebo) as provided in the study. We examined the differences in these rates to determine the treatment effect bias, as differences in rates of missing data between the groups are indicative of data not missing at random. This would indicate a high risk of bias for incomplete outcome reporting in the included study. This is reported in the risk of bias.
Assessment of heterogeneity
We were unable to assess heterogeneity, as we only included one study in the review (see Baker 2017; Table 1).
Assessment of reporting biases
We were unable to assess reporting biases, as we only included one study in the review (see Baker 2017; Table 1).
Data synthesis
We were unable to conduct a meta‐analysis as we only included one study in the review (see Baker 2017; Table 1).
Subgroup analysis and investigation of heterogeneity
We were unable to conduct a subgroup analysis or investigate heterogeneity, as we only included one study in the review (see Baker 2017; Table 1).
Sensitivity analysis
We were unable to conduct a sensitivity analysis, as we only included one study in the review (see Baker 2017; Table 1).
Summary of findings table
Following the recommendations in section 11.5.4 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2017), and using GRADEprofiler: Guideline Development Tool (GRADEpro GDT 2015), we created a 'Summary of findings' table for the comparison, trihexyphenidyl versus placebo for dystonia in cerebral palsy. We reported the following outcomes in the table: change in dystonia; adverse effects; participation in activities of daily living; and quality of life. We reported all outcomes at 12 weeks follow‐up except for adverse effects, whose analysis contains data assessed at both 12 and 28 weeks because we were unable to separate the data.
Two review authors (AH and KW) independently assessed the quality of the evidence for each outcome contributing data using the GRADE tool (GRADE 2004), looking at study limitations, consistency of effect, imprecision, indirectness and publication bias.
Results
Description of studies
A description of the included study is in the Characteristics of included studies table.
Results of the search
We conducted a literature search up to 26 May 2017, identifying 128 original records. After screening of titles and abstracts, we retrieved three full‐text reports. We excluded one study, Reddihough 1990, because it was not an RCT (see Excluded studies; Characteristics of excluded studies table). We identified two reports of one original trial for inclusion (Rice 2009). Figure 1 shows a study flow diagram.
Study flow diagram.
Included studies
Study design
Rice 2009 was a randomised, double‐blind, placebo‐controlled, cross‐over trial.
Participants
The study recruited 16 children with predominant dystonic cerebral palsy and a mean age of nine years (SD 4.3 years, range 2 to 17 years). There were 10 boys and 6 girls.
Diagnosis
One of the study physicians verified the diagnosis of dystonia, but authors did not report the method used.
Randomisation
Children were randomised into either trihexyphenidyl (dose starting at 0.2 mg/kg/d in three divided doses and increased over six weeks up to a maximum 2.5 mg/kg/d in three divided doses) or placebo (liquid delivered orally at 2.5 mg/kg/day of liquid in three divided doses (equals same volume as intervention)) for 12 weeks. Parents administered the trihexyphenidyl and the placebo. There was a washout period of four weeks prior to cross‐over.
Outcomes
The primary outcomes reported were change in dystonia from baseline, assessed using the Barry Albright Dystonia Scale (BADS) and adverse effects. Authors counted all side effects as adverse effects. Secondary outcomes reported were upper limb function, assessed using the Quality of Upper Extremity Skills Test (QUEST) and participation in activities of daily living at home, school and in the community, assessed using the Canadian Occupational Performance Measure (COPM) and the Goal Attainment Scale (GAS). Trialists did not measure pain or quality of life. Children were assessed at baseline, 12 weeks and 28 weeks after commencement. We only included data from the first phase (12 weeks) in this review, except for adverse effects where it was not possible to separate first‐ and second‐phase data.
Excluded studies
We excluded one study, Reddihough 1990, because it was not an RCT. See the Characteristics of excluded studies table.
Risk of bias in included studies
Figure 2 presents a summary of the 'Risk of bias' assessment for the included trial, Rice 2009. We judged the trial as being at low risk of bias for all categories.
Risk of bias summary: review authors' judgements about each risk of bias item for each included study.
Allocation
We considered Rice 2009 to be at low risk of selection bias due to both random sequence generation and allocation concealment because the trial pharmacy generated a randomisation table and kept codes concealed until after data collection was complete.
Blinding
We judged Rice 2009 to be at low risk of performance and detection bias because assessors, the patient and the family were all blinded to the intervention.
Incomplete outcome data
We judged Rice 2009 to be at low risk of attrition bias because, although two of the eight children who received the active treatment in the first phase dropped out, one child withdrew due to a family crisis unrelated to the medication.
Selective reporting
We judged Rice 2009 to be at low risk of reporting bias because it reported on all pre‐specified outcomes.
Other potential sources of bias
We identified no other potential sources of bias for Rice 2009.
Effects of interventions
In order to obtain the first‐phase data only, we contacted the study authors and they provided the requested information. The follow‐up time point for the first phase was 12 weeks.
Primary outcomes
Change in dystonia from baseline
Our analysis of first‐phase data only showed no evidence of a difference in mean follow‐up scores, with an estimate that the BADS score (eight body regions assessed for dystonia on a five‐point scale (0 = none to 4 = severe), for a total score of 0 to 32) was 2.67 points higher (95% CI −2.55 to 7.90; low‐quality evidence; Figure 3), that is, worse dystonia, in the treated group.
ANCOVA analyses, page 1
The results reported by the study authors from both phases using the general linear model analysis showed no evidence that trihexyphenidyl had any treatment (F(1,12) = 0.2, P = 0.67), carry‐over (F(1,12) = 1.7, P = 0.22) or order (F(1,12) = 0.3, P = 0.57) effects.
Adverse effects
The study authors reported that trihexyphenidyl increased the risk of adverse effects by 154% using data from both the first and second phases of the study. All children had reported adverse effects in the treatment phase (16/16), so all children receiving treatment in the first phase experienced adverse effects (8/8). Reported adverse effects included agitation, constipation, dry mouth and poor sleep. Authors reported that 6 out of 16 participants had adverse effects in the placebo phase; however, the timing of these effects is not clear. It is conceivable that children who received the placebo in the second phase may have experienced ongoing adverse effects related to the treatment phase.Therefore, the estimate of the number of adverse effects with placebo in the first phase may be lower than three out of eight, and we may be underestimating the increased risk with treatment.
Secondary outcomes
Activity
Our analysis of first‐phase data only showed no evidence of a difference in mean follow‐up scores as measured by the QUEST (36 items across four domains, scored one or two, producing a score of 0 to 100), with an estimated score of 4.62 points lower (95% CI −10.98 to 20.22; low‐quality evidence), that is worse upper limb function, in the treated group.
The results reported by the study authors from both phases using general linear model analysis showed no evidence that trihexyphenidyl had any treatment (F(1,12) = 0.9, P = 0.37), carry‐over (F(1,12) = 1.4, P = 0.25) or order (F(1,12) = 0.2, P = 0.90) effects.
Participation in activities of daily living
Our analysis of first‐phase data only showed a difference in mean follow‐up scores, as measured by three tools, in the treated group, with an estimate of: 18.86 points higher (95% CI 5.68 to 32.03; low‐quality evidence) for the GAS (up to five functional goals scored on 5‐point scale (−2 = much less than expected to +2 = much more than expected)), 2.91 points higher (95% CI 1.01 to 4.82; low‐quality evidence) for the satisfaction subscale of the COPM (satisfaction with performance in up to five problem areas scored on a 10‐point scale (1 = not satisfied at all to 10 = extremely satisfied)), and 2.24 points higher (CI 95% 0.64 to 3.84; low‐quality evidence; Figure 4) for the performance subscale of the COPM (performance in up to five problem areas scored on a 10‐point scale (1 = not able to do to 10 = able to do extremely well)). Higher scores represent improved participation.
ANCOVA analyses, page 2
The results reported by the study authors from both phases using general linear model analysis showed no evidence that trihexyphenidyl had any treatment or carry‐over effects for any of the three participation measures but had statistically significant order effects on the GAS (F(1,11) = 10.2, P = 0.009) and borderline significant order effects on the performance component of the COPM (F(1,12) = 4.7, P = 0.05).
Pain and quality of life
Rice 2009 did not report on these outcomes.
Quality of the evidence
Although we judged Rice 2009 to be at low risk of bias in all categories, we considered the quality of the evidence for all reported outcomes to be low after downgrading two levels due to imprecision resulting from the inclusion of a single small study.
Discussion
Summary of main results
For our primary outcomes, the results of our analysis using phase‐one data only from the one included cross‐over trial did not generate evidence that trihexyphenidyl reduces dystonia but did identify that the risk of adverse effects is high. For the secondary outcomes, there was no evidence that trihexyphenidyl increases upper limb function, but there was improved goal attainment relating to improved participation in activities of daily living. There was a lack of internal consistency with the expectation that improvement in goal attainment and participation would be mediated by reduced dystonia. The study did not measure pain or quality of life.
The risk for adverse effects needs to be interpreted with caution, as we were unable to separate out first‐ and second‐phase data. Consequently, we may have underestimated the risk for adverse effects with treatment.
There were slight differences in the results from our analyses using phase‐one data only compared with the published authors' analyses of combined phases. Using the phase‐one data, we observed differences between the treatment and placebo scores that were in the same direction as the published authors’ analyses, but greater in magnitude. In addition, our results found a difference in COPM performance and satisfaction scales compared to the study authors. This suggests that the magnitude of the treatment effect was smaller in the second phase than in the first phase of the trial. It is not possible to determine whether this difference between analyses is due to small carry‐over effects, to chance or to the small numbers of participants in the trial.
Overall completeness and applicability of evidence
The evidence base for trihexyphenidyl in managing dystonia in people with cerebral palsy is incomplete. The only RCT we could find assessed the outcomes of dystonia reduction, adverse effects, upper limb function and goal attainment related to improved function and participation in a small sample of children and young people aged 2 to 17 years, who either walk with assistive devices or are non‐ambulant. No RCTs have evaluated pain, quality of life, or outcomes for adults with dystonic cerebral palsy or higher gross motor function.
Quality of the evidence
Using the GRADE criteria (GRADE 2004; Schünemann 2017), we rated the quality of the evidence for all outcomes as low, due to the small sample size and lack of any other RCT, leading to imprecision and inconsistency. Consequently, our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect.
Potential biases in the review process
We conducted an extensive search of all available literature, including grey literature. We included trials regardless of publication date or language. Therefore, we are confident that this review includes all published evidence from RCTs on this topic to date. By including only RCTs, we excluded a small number of non‐randomised studies that examine trihexyphenidyl in cerebral palsy; however, these studies do not add to the quality of evidence for this intervention. One author of this review (DSR) is a co‐author of a published study that we excluded from the review, and three review authors (AH, AS and DSR) collaborate with authors of the included published trial. Independent review authors assessed the eligibility, risk of bias and quality of the evidence for this study.
Agreements and disagreements with other studies or reviews
There is little literature with which to compare the results of this review. Our results are consistent with a recent systematic review of the efficacy of oral pharmacological treatments in dyskinetic cerebral palsy. That review also included the study by Rice 2009, which met our eligibility criteria (Criteria for considering studies for this review), concluding that "trihexyphenidyl needs further investigation, primarily in dystonic patients with predominant involvement of upper limb" (Masson 2017).
Other non‐randomised studies have reported inconsistent results from studies examining trihexyphenidyl in cerebral palsy. In contrast to our review, a prospective, open‐label, multicentre pilot trial of high‐dose trihexyphenidyl in 23 children aged 4 to 15 years with cerebral palsy and dystonia impairing function in the dominant upper extremity found some improvement in upper limb function (Sanger 2007). However post hoc analyses indicated that a subgroup of children with hyperkinetic dystonia worsened over this period. Similar to our review, Sanger 2007 reported no effect for reducing dystonia or improving gross motor function, quality of life, or care and comfort. Retrospective chart reviews have reported results inconsistent with ours: Carranza del Rio 2011 reported reduction of dystonia, and Ben‐Pazi 2011 and Hoon 2001, improvements in motor function; however, methodological issues and inconsistent outcome reporting lower the quality of these results. Also, higher positive outcomes can be expected when using retrospective data. Although these non‐randomised studies add to the body of literature for trihexyphenidyl in dystonia in cerebral palsy, their results need to be interpreted with caution due to the low quality of the evidence.
Consistent with our review, all studies reported a high incidence of adverse effects.
Study flow diagram.
Risk of bias summary: review authors' judgements about each risk of bias item for each included study.
ANCOVA analyses, page 1
ANCOVA analyses, page 2
Comparison 1 Trihexphenidyl versus placebo, Outcome 1 Adverse effects.
| Trihexyphenidyl compared with placebo for dystonia in cerebral palsy | |||||
| Patient or population: children with dystonic cerebral palsy Settings: one tertiary care hospital Intervention: trihexyphenidyl Comparison: placebo | |||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | Number of participants | Quality of the evidence | |
| Assumed risk | Corresponding risk | ||||
| Placebo | Trihexyphenidyl | ||||
| Change in dystonia from baseline Measured by: BADS (eight body regions assessed for dystonia on a five‐point scale (0 = none to 4 = severe), minimum score 0 to maximum score 32; higher score = greater severity of dystonia) Follow‐up: 12 weeks | The mean follow‐up score in the control group was 15.50 points | The mean follow‐up score in the intervention group was 2.67 points higher (2.55 lower to 7.90 higher) | — | 16 | ⊕⊕⊝⊝ Lowa |
| Adverse effectsb (mood disturbance, irritability, behavioural change, constipation) Measured by: counts of number and type Follow‐up: various (includes data assessed at both 12 and 28 weeks) | 375 per 1000 | 1000 per 1000 | RR 2.54 (1.38 to 4.67) | 16 | ⊕⊕⊝⊝ |
| Participation in activities of daily living:individual goal setting Measured by: GAS (up to 5 functional goals scored on a 5‐point scale (−2 = much less than expected to +2 = much more than expected); higher score = better than expected outcome) Follow‐up: 12 weeks | The mean follow‐up score in the control group was 27.63 points | The mean follow‐up score in the intervention group was 18.86 points higher (5.68 higher to 32.03 higher) | — | 16 | ⊕⊕⊝⊝ |
| Participation in activities of daily living:satisfaction with individual goals Measured by: satisfaction subscale of the COPM (satisfaction with performance in up to 5 problem areas scored on a 10‐point scale (1 = not satisfied at all to 10 = extremely satisfied); higher score = greater satisfaction) Follow‐up: 12 weeks | The mean follow‐up score in the control group was 2.96 points | The mean follow‐up score in the intervention group was 2.91 points higher (1.01 higher to 4.82 higher) | — | 16 | ⊕⊕⊝⊝ |
| Participation in activities of daily living:performance of individual goals Measured by: performance subscale of the COPM (up to five problem areas scored on a 10‐point scale (1 = not able to do to 10 = able to do extremely well; higher score = better performance) Follow‐up: 12 weeks | The mean follow‐up score in the control group was 3.14 points | The mean follow‐up score in the intervention group was2.24 points higher (0.64 higher to 3.84 higher) | — | 16 | ⊕⊕⊝⊝ |
| Quality of life | Not measured | ||||
| *The basis for the assumed risk is provided in the footnotes. The corresponding risk (and its 95% CI) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI) | |||||
| GRADE Working Group grades of evidence | |||||
| aDowngraded two levels due to imprecision; small sample size from one study only. | |||||
| Method | Unused methods |
| Measures of treatment effect | Continuous data For continuous outcomes we will calculate the MD and corresponding 95% CI if studies use the same rating scales. We will calculate the SMD with 95% CIs if studies use different scales to measure the same outcomes. As recommended in section 9.4.5.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017), we will focus on final values unless some of the studies use change scores. We will combine studies that report final values with studies that report only change scores in the same meta‐analysis, provided that the studies use the same rating scale. We will conduct the analysis according to age, as children and adults respond differently to medication. We will combine the data from all groups in studies that have trihexyphenidyl in more than one group (i.e. different frequencies) and then separate these when performing the subgroup analysis to see how the different frequencies influence the results (see item four in the Subgroup analysis and investigation of heterogeneity section). |
| Multiple outcomes If studies provide multiple, interchangeable measures of the same construct at the same point in time, we will calculate the average SMD across the outcomes and the average estimated variances, as recommended in section 16.1.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). | |
| Unit of analysis issues | Cluster‐RCTs If included trials use cluster randomisation, we will extract an ICC and use this to reanalyse the data. Where no ICC is given and a unit of analysis error appears to exist, we will contact the trial authors and ask them to provide either an ICC or the raw data to enable calculation of an ICC. Where no ICC is made available, we will search for similar studies from which we can impute an ICC, or seek statistical advice to obtain an estimate of the ICC. |
| Dealing with missing data | We will contact trial investigators to request missing data. If the trialists provide missing data, we will conduct a meta‐analysis according to intention‐to‐treat principles using all data and keeping participants in the treatment group to which they were originally randomised, regardless of the treatment they actually received, as recommended in section 16.1.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). If missing data are not provided, we will analyse only the available data. If there is concern regarding a high level of missing data, such that data could not be included in a meta‐analysis, we will include a qualitative summary in the text of the review. We will document missing data and attrition in the 'Risk of bias' tables, and we will explore how missing data might affect the interpretation of the results by conducting a sensitivity analysis. |
| Assessment of heterogeneity | We will assess clinical heterogeneity by comparing the between‐trials distribution of participant characteristics (e.g. children versus adults) and intervention characteristics (e.g. treatment type and dose), and assess methodological heterogeneity by comparing trial characteristics (e.g. cross‐over versus parallel design). We will evaluate statistical heterogeneity using the I2 statistic and the Chi2 test of heterogeneity, with statistical significance set at P value < 0.10. As recommended in section 9.5.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017), we will consider I2 values as follows.
We will report Tau2 as an estimate of the between‐study variance when reporting the results from the random‐effects model. |
| Assessment of reporting biases | If we identify 10 or more studies, we will use funnel plots to investigate the relationship between intervention effect and study size. We will explore possible reasons for any asymmetry found. We will analyse the funnel plot of the data to ascertain asymmetry. Asymmetry of a funnel plot may indicate, among other things, publication bias or poor methodological quality (Egger 1997). |
| Data synthesis | We will synthesise results in a meta‐analysis using a fixed‐effect model when studies are similar enough with regard to the intervention, population and methods, to assume that the same treatment effect is estimated. We will synthesise results in a meta‐analysis using a random‐effects model when statistical heterogeneity is found or when studies differ enough with regard to the intervention, population, and methods, to assume that different yet related treatment effects are estimated, and when it is deemed to be clinically relevant, as recommended in section 9.4.3.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017). |
| Subgroup analysis and investigation of heterogeneity | We will conduct the subgroup analyses listed below.
We will also look at the number of participants per study to determine if this is sufficient to perform a subgroup analysis. |
| Sensitivity analysis | We will conduct sensitivity analyses to investigate the effect on the overall results of excluding trials that meet the criteria described below.
We will also conduct a sensitivity analysis for studies with very low risk of bias. In addition, we will conduct a sensitivity analysis using a range of ICCs to assess the impact on treatment effect. |
| CI: confidence intervals; ICC: intraclass correlation coefficient; MD: mean difference; SMD: standardised mean difference. | |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Adverse effects Show forest plot | 1 | Risk Ratio (M‐H, Fixed, 95% CI) | Totals not selected | |
