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Cochrane Database of Systematic Reviews Protocol - Intervention

Bisphosphonate use in children with cerebral palsy

Authors' declarations of interest

Version published: 28 August 2017 Version history

https://doi.org/10.1002/14651858.CD012756

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view the current version 05 July 2021
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Abstract

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

To examine the efficacy and safety of bisphosphonate therapy in the treatment of low BMD or secondary osteoporosis (or both) in children with cerebral palsy (GMFCS Levels III to V) who are under 18 years of age.

Background

Cerebral palsy is a heterogeneous group of non‐progressive disorders of posture or movement, due to a lesion of the developing brain. Cerebral palsy is the most common form of childhood disability, with worldwide incidence rates between 2 and 2.5 per 1000 live births (Pharoah 1998; Reddihough 2003; Stanley 2008). The prevalence of severe cerebral palsy in Europe, defined by an inability to walk, coupled with severe intellectual disability, is approximately 0.43 per 1000 live births (SCOPE 2002).

Several risk factors are involved in the development of cerebral palsy, which can occur during pregnancy, at birth, or after birth. These include maternal infections, premature birth, low birth weight, disruption of oxygen or blood supply to the brain, and infections or injury in the neonatal period and in early childhood, resulting in abnormalities in brain development that lead to cerebral palsy.

Description of the condition

Osteoporosis is common in children with cerebral palsy. Osteoporosis is a condition characterised by reductions in bone strength, leading to an increased risk of fractures (NIH 2001). Around 80% to 90% of children with severe cerebral palsy have low bone mineral density (BMD) and an increased risk of fragility fractures. Many of those who sustain a fracture will sustain repeated fractures (Henderson 2002; Mergler 2009). The most common site of fracture is the femur. Prevalence of femur fractures has been variably estimated at 20% in non‐ambulant children and young adults with cerebral palsy (Henderson 2002). The incidence of fracture in children with severe cerebral palsy has been reported as 7% to 9.7% per year (Stevenson 2006). Severe cerebral palsy is defined as Level IV or V, according to the Gross Motor Function Classification System (GMFCS), and a history of clinically‐diagnosed cerebral palsy (Palisano 2000; Reid 2011). The GMFCS is a tool used frequently in children with cerebral palsy, which assesses the independent mobility and function of children according to chronological age (Palisano 2000). A full description of the GMFCS is presented in Appendix 1.

The cause of low BMD in children with severe cerebral palsy is multifactorial, including impaired weight‐bearing mobilisation, less exposure to sunlight, poor growth and nutrition, and anticonvulsant use. Bone mineralisation is also adversely affected by the use of anticonvulsants (Henderson 2002). The most commonly used method to asses BMD in children is dual x‐ray absorptiometry (DXA). This offers many practical advantages, including rapid scanning time, easy and wide availability, and low use of radiation (Boyce 2014). The results of DXA are expressed as Z scores, calculated from age, gender, and ethnicity‐adjusted norms, and are derived from normative databases specific to the brand of densitometer used (Zemel 2011).

Treatment involves conservative measures, including optimising the management of underlying conditions, maintaining appropriate calcium and vitamin D intake, encouraging weight‐bearing physical activity, and medications, such as bisphosphonate. Guidelines published for the management of bone health in this population have reported probable evidence for bisphosphonate, possible evidence for vitamin D and calcium, and not enough evidence for weight‐bearing activities, as effective interventions to improve BMD (Fehlings 2012). Important effects on low BMD have been observed in small and diverse cohorts of children with cerebral palsy, using both a medical and a physical approach (Cohran 2013). However, it is unclear whether small sample sizes or variable treatment responses account for the non‐significant findings, thus additional, large randomised controlled trials (RCTs) are needed (Hough 2010).

Description of the intervention

Bisphosphonates increase BMD and reduce fracture rates by inactivating osteoclasts (large multinucleated cells that degrade or reabsorb bone), which are responsible for the breakdown of existing bone cells. Bisphosphonates are used widely in the treatment of adult osteoporosis, but their use in children is controversial because of a lack of long‐term safety and efficacy data (Allington 2005; Boyce 2014).

It should be noted that the primary defect of bone in cerebral palsy is a limitation in bone formation, which would respond best to anabolic therapies, for example, teriparatide. However, current guidelines do not support the use of anabolic therapies in growing bone, due to concerns related to osteosarcoma, which was identified in rats in a clinical trial setting (Vahle 2002). Thus, bisphosphonate remain the most practical alternative therapy available to children with cerebral palsy for the treatment of osteoporosis.

Very few short‐term side effects have been reported with bisphosphonate use. Many studies have reported symptoms, including fever, malaise and flu‐like symptoms, after the first infusion of bisphosphonate. In addition, children have also experienced gastrointestinal symptoms, including nausea, vomiting, and abdominal pain. Other possible adverse effects reported were hypocalcaemia, hypophosphataemia, bone pain, transient uveitis, acute renal tubular necrosis, nephrocalcinosis, and delayed fracture healing. Duration of bisphosphonate use is an important factor, as long‐term use (more than five years) in adults has been associated with increased incidence of atypical femoral fractures (Shane 2013). Osteonecrosis of the jaw has also been linked with long‐term use, and with use in settings with poor dental hygiene (Khosla 2007).

Cochrane reviews by Dwan 2014 and Ward 2007 concluded that there were insufficient data to support the use of bisphosphonate as standard therapy in children. However, over the past few decades, bisphosphonate use in children has increased, especially in the treatment of osteogenesis imperfecta (OI). Dwan 2014 included RCTs that provided evidence of the efficacy of bisphosphonate in improving BMD, reducing fracture risk, and improving pain in children with OI.

How the intervention might work

Bisphosphonates are synthetic analogues of pyrophosphate, an endogenous regulator of bone metabolism. They increase BMD by inhibiting osteoclast activity. Bisphosphonate can be administered via the oral (PO) or intravenous (IV) route, but as oromotor dysfunction or gastrointestinal reflux (or both) are often associated with cerebral palsy, PO administration may not be safe or advisable in this group (Sullivan 2008). Thus, it is preferable to use IV formulations of bisphosphonate in the treatment of osteoporosis in children with cerebral palsy.

Clinical issues under consideration that relate to the use of bisphosphonate include the choice of therapeutic regimen (e.g. the use of intermittent dosing rather than continuous, IV dosing versus PO therapy), the optimal duration of therapy, the combination with other drugs, such as teriparatide, and their extended use in other related conditions, including glucocorticosteroid‐associated osteoporosis, childhood osteopenic disorders, arthritis, etc. (Russell RG 2011).

Several bisphosphonates are available for use in adults, including etidronate (Didronel), pamidronate (Aredia), alendronate (Fosamax), ibandronate (Boniva), and risedronate (Actonel), but few are effective and safe to use in children. Pamidronate, in particular, has proved remarkably effective in increasing bone in children with the inherited 'brittle‐bone' disorder, OI. Both pamidronate and risedronate have been used in controlled trials of bisphosphonate conducted with children with cerebral palsy (Henderson 2002; Iwasaki 2008; Iwasaki 2011).

In a RCT, children with nonambulatory cerebral palsy were reported to benefit from treatment with pamidronate (bisphosphonate). The study reported an average 89% increase in BMD in the distal femur in children treated with intravenous bisphosphonate over a 18‐month study period, compared with a 9% increase in BMD in the placebo group (Henderson 2002).

Why it is important to do this review

Osteoporosis is common in children with cerebral palsy. Around 80% to 90% of nonambulatory children with severe cerebral palsy have low BMD, and the incidence of fragility fractures is very high (Henderson 2002;Mergler 2009). Fractures diminish the quality of life of these children.

Current guidelines do not support the use of anabolic therapies in children for treating osteoporosis, due to concerns related to osteosarcoma, which was identified in rats in a clinical trial setting (Vahle 2002). Thus, bisphosphonate remain the most practical, bone‐altering therapy available to children with cerebral palsy for the treatment of osteoporosis. Although bisphosphonate remains a promising treatment, there is no consensus regarding the timing, dose, or duration of treatment. Therefore, there is a need for evidence‐based guidelines and a review of studies related to bisphosphonate use in this population.

Objectives

To examine the efficacy and safety of bisphosphonate therapy in the treatment of low BMD or secondary osteoporosis (or both) in children with cerebral palsy (GMFCS Levels III to V) who are under 18 years of age.

Methods

Criteria for considering studies for this review

Types of studies

All randomised controlled trials (RCTs) and quasi‐RCTs that implemented bisphosphonate in the treatment of low BMD or secondary osteoporosis (or both) in nonambulatory children and adolescents with cerebral palsy.

Types of participants

Children under 18 years of age with cerebral palsy (GMFCS Levels III to V).

We will not include data from studies that do not differentiate between children with osteogenesis imperfecta (OI) and idiopathic juvenile osteoporosis (IJO), and children with osteoporosis due to other conditions.

Types of interventions

Oral or IV administration of at least one bisphosphonate (e.g. alendronate, pamidronate, etidronate, clodronate, tiludronate, olpadronate, incadronate, risedronate, zoledronate, or a combination), given at any dose, to treat low BMD or osteoporosis in children with cerebral palsy, compared with placebo or no drug.

Types of outcome measures

Primary outcomes

  • Improvement or change in areal BMD Z‐score of the lumbar spine, total body less head, or lateral distal femur, as measured by dual x‐ray absorptiometry (DXA scan).

  • Improvement in volumetric BMD of distal tibia or radius, using peripheral, quantitative computerised tomography (pQCT).

  • Fracture frequency: number of incident fractures (clinical, radiographic, or both) noted per participant per year before and after bisphosphonate treatment.

  • Adverse effects associated with bisphosphonate use as experienced by children (which will include acute symptoms (fever, chills, malaise); gastrointestinal symptoms, including nausea, vomiting, and abdominal pain; or possible sequelae, including hypocalcaemia, hypophosphataemia, bone pain, transient uveitis, nephrocalcinosis, acute tubular necrosis, delayed fracture healing, and death).

Secondary outcomes

  • Changes in serum or urine bone markers, such as bone‐specific alkaline phosphatase, osteocalcin, and N‐telopeptides, before and after bisphosphonate treatment, to ascertain whether bone turnover is impacted or overly suppressed.

  • Bone pain and quality of life, as reported by the participant or the child’s parents, before and after bisphosphonate use.

We will include studies that use any validated scale that measures the primary and secondary outcomes listed above.

We will collect primary outcomes for the following time points: short‐term (zero to less than one month postintervention), intermediate‐term (one month to less than six months postintervention), and long‐term (equal to or greater than six months postintervention).

We will include all of our outcomes a 'Summary of findings' table.

Search methods for identification of studies

Electronic searches

We will search the following electronic databases and trial registers for all available years.

  • Cochrane Central Register of Controlled Trials (CENTRAL; current issue) in the Cochrane Library, and which includes the Cochrane Developmental, Psychosocial and Learning Problems Group Specialised Register.

  • MEDLINE Ovid (1946 to current).

  • MEDLINE In‐Process and Other Non‐Indexed Citations Ovid (current issue).

  • MEDLINE E‐Pub ahead of Print Ovid (current issue).

  • Embase Ovid (1974 to current).

  • CINAHL Plus EBSCOhost (Cumulative Index to Nursing and Allied Health Literature; 1937 to current).

  • Cochrane Database of Systematic Reviews (CDSR; current issue) part of the Cochrane Library.

  • Database of Abstracts of Reviews of Effects (DARE; current issue) part of the Cochrane Library.

  • Epistemonikos (www.epistemonikos.org; all available years).

  • Science Citation Index Web of Science (SCI; 1970 to current).

  • Conference Proceedings Citation Index ‐ Science Web of Science (CPCI‐S; 1990 to current).

  • Clinicaltrials.gov (clinicaltrials.gov; all available years).

  • World Health Organization International Clinical Trials Registry Platform (WHO ICTRP; apps.who.int/trialsearch; all available years).

We will search MEDLINE using the search strategy in Appendix 2, which we will then adapt, as appropriate, for other sources. We will not limit the searches by language, date, or publication status.

Searching other resources

We will also search the reference lists of relevant systematic reviews, trials, and case studies identified by the search. We will contact the authors of potentially relevant studies, and companies that manufacture bisphosphonate, in an attempt to identify unpublished literature.

Data collection and analysis

Selection of studies

Two review authors (ZZ and EM) will independently check the titles and abstracts of all records yielded by the search (Electronic searches), and exclude those that do not meet the inclusion criteria outlined above (Criteria for considering studies for this review). In cases that appear to meet the inclusion criteria, or where there is any doubt as to whether the record should be excluded, both review authors will retrieve the full text of the report and assess it for eligibility. Any disagreements will be resolved by discussion or, if necessary, by consulting a third review author (CM or DM). We will record our decisions in a PRISMA diagram (Moher 2009).

Data extraction and management

Two review authors (ZZ and EM) will independently extract the following data, using a standardised form developed for this purpose:

  • study design;

  • sample size: treatment and control groups;

  • study population (treatment and control groups): sex, age, ambulatory or nonambulatory cerebral palsy gross motor function (GMFCS Level), and any previous fracture;

  • intervention: type of intervention, bisphosphonate PO or IV, dosage and duration of treatment, monotherapy or multiple treatment (e.g. calcium and vitamin D or alfacalcidol);

  • outcome measures: improvement in BMD, fracture rate, adverse effects, changes in serum or urine bone markers, bone pain and quality of life (Types of outcome measures);

  • potential conflicts of interest; and

  • stated/declared conflicts of interest.

Both review authors will resolve disagreements regarding the extraction of data by discussion. If they cannot reach a resolution, they will consult a third review author (CM).

We will conduct the data analyses using Review Manager 5 (RevMan 5) software (Review Manager 2014).

Assessment of risk of bias in included studies

Using Cochrane’s 'Risk of bias' tool (Higgins 2011a), two review authors (from ZZ, EM, DM and CMD) will independently assess each study for risk of bias across the following domains:

  • random sequence generation: was the allocation sequence adequately generated?

  • allocation concealment: was allocation adequately concealed?

  • blinding of participants and personnel: was knowledge of the allocated intervention adequately prevented during the study?

  • blinding of outcome assessment: was knowledge of the allocated intervention adequately prevented during the study?

  • incomplete outcome data: were incomplete outcome data adequately addressed?

  • selective reporting: are reports of the study free of suggestion of selective outcome reporting? and

  • other sources of bias: was the study apparently free of other problems that could put it at a high risk of bias?

We will assign each study a rating of high, low, or unclear (ambiguous) risk of bias for each domain; the criteria for these judgements are provided in Appendix 3. We will discuss any disagreements until a consensus is reached. If we rate one or more domain(s) as being at high risk of bias, we will judge the study to be at high risk of bias overall; we will only rate a study as being at low risk of bias overall if we rate it as such for all domains.

We will present our judgements with reasons in a 'Risk of bias' table.

Measures of treatment effect

Binary data

For dichotomous data, we will calculate the effect size as a risk ratio (RR), and present it with 95% confidence intervals (Cl). We will consider a change as an improvement in BMD of the femur (lateral or distal), lumbar spine, and total body less head, as measured by (DXA), or volumetric BMD measured by pQCT.

Continous data

Where included studies have assessed the same continuous outcome using the same scale, we will present the effect size as a mean difference (MD) with 95% CI. We will use the standardised mean difference (SMD) with 95% CI if outcomes for the same purpose are measured by different scales.

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 (Borenstein 2009).

The aim here is to prevent studies that report on more outcome measures from receiving more weight in an analysis than studies that report on only a single outcome measure.

The effect estimate can be presented as a MD, by transforming the SMD effect estimate backwards to one of the well‐known scales, together with a pre‐defined Minimal Clinically Important Difference (MCID).

Unit of analysis issues

Cluster‐randomised trials

We will seek direct estimates of the effect from an analysis that accounts for the cluster design. When the analysis does not account for the cluster design in the cluster trial, we will use the approximately correct analysis approach, as presented in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b).

We can perform approximately correct analyses if we can extract data on (1) the number of clusters randomised to each intervention group, or the mean size of each group or cluster, (2) the outcome data, ignoring the cluster design, for the total number of individuals (e.g. number of participants with events or means, and standard deviations (SD)), and (3) an estimate of the intra‐cluster (or intra‐class) correlation coefficient (ICC).

We will calculate the ‘effective sample size’ for each cluster trial (Rao 1992), using the method described by Higgins 2011b. In cases where the ICC is not available from the study report, we will try to contact the authors, or obtain external estimates from similar studies or resources (Campbell 2000). If we are still unable to identify an appropriate ICC, we will conduct sensitivity analyses using a range of possible ICCs (0.20, 0.10, 0.05, 0.01). We will enter these data into a meta‐analysis using the generic inverse‐variance method (Higgins 2011c).

Cross‐over trials

Only when the data are clear of carry‐over effects will we include cross‐over trials in the meta‐analysis. We will combine the results of cross‐over studies with those of parallel studies by imputing the correlation coefficient from an included study that presents individual participant data, and use this to calculate the standard deviation. We will use the generic inverse variance method to conduct a meta‐analysis of this data (Higgins 2011b). To avoid presenting repeated measurements reported in a study, we will only include data from one time point from an individual study in any single meta‐analysis.

Studies with multiple treatment groups

We will combine all relevant intervention groups and compare them with all relevant control groups, making single pair‐wise comparisons. If this approach does not allow for investigation of intervention‐related sources of heterogeneity, we will include each intervention arm in separate pair‐wise comparisons, halving the sample size for the control group so to avoid double counting of participants. For dichotomous outcomes, we will add the number of participants with intervention and the total number of participants, across the groups (Higgins 2011b). In case of continuous outcomes, we will combine the mean and SD using the formulae described in Chapter 7 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011d).

Dealing with missing data

We will identify and report missing data (dropouts, withdrawals, missing summary data) in the 'Characteristics of included studies' and 'Risk of bias' tables.

We will request missing data from study authors. If data are made available, we will include them in the analyses. In case of no response from the authors, we will send two reminder requests at monthly intervals. If still there is still no response and data remain unavailable, we will:

  • calculate missing summary data (such as missing SDs) from CIs, standard errors, P values or t values, where possible, using the methods provided in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b);

  • carry the last observation forward (LOCF) for missing continuous data; and

  • in the case of missing dichotomous data, assume that all missing participants experienced the event.

We will specify the methods used to estimate the data in the 'Characteristics of included studies' tables and perform a Sensitivity analysis to compare the results of analyses with imputed missing data to those without imputed missing data. Where imputation is not possible, we will explain this in the text, and conduct an available‐case analysis. We will discuss the possible impact of the missing data on the results in the Discussion section.

Assessment of heterogeneity

We will assess the following types of heterogeneity:

  • clinical heterogeneity, including variability in participants, for example, age, gender, rate of fracture and functional ability (based on GMFCS), and characteristics of the interventions or setting;

  • methodological heterogeneity (variation in study designs); and

  • statistical heterogeneity (variation in intervention effects).

We will assess clinical heterogeneity within each pair‐wise comparison by inspecting each included study for any differences or variations seen in the participants, interventions, or outcomes described. We will assess methodological heterogeneity within each pair‐wise comparison by evaluating each included study for any variability in the study design and risk of bias.

We will assess statistical heterogeneity between studies by visual inspection of the forest plot for overlapping CI, using the Chi2 test for homogeneity with a significance level of α (alpha) = 0.1, and calculating the I2 statistic for quantifying inconsistency (estimating the percentage of variation in effect estimates due to heterogeneity rather than sampling error). We will judge I2 values based on the thresholds listed below, as suggested in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011c):

  • 0% and 40%: may indicate little heterogeneity;

  • 30% and 60%: may indicate moderate heterogeneity;

  • 50% and 90% may indicate substantial heterogeneity; and

  • 75% and 100% may indicate considerable heterogeneity.

These thresholds can be misleading. Therefore, when considering the importance of I2, we will take into account the size and direction of effects, and the strength of evidence for heterogeneity based on the P value from the Chi2 test or a CI for I2. We will also estimate and present Tau2, along with its CI to provide an estimate of the amount of between‐study variation.

Assessment of reporting biases

Where data from a sufficient number of studies are available (at least 10 studies in a meta‐analysis), we will draw funnel plots and test for funnel plot asymmetry (Egger 1997). If we find any asymmetry of the funnel plot, we will look for possible causes (such as publication bias or true heterogeneity). This may be considered a likely influence on the observed effect sizes in our interpretation of the results. However, given that common tests of publication bias lack sensitivity, where indicated, we will consider the possible influence that a dominance of small trials might have on pooled effect sizes in our interpretation.

Data synthesis

We will use Review Manager 2014 to conduct our statistical analyses. As we expect some heterogeneity in intervention characteristics, we will pool the available data using the random‐effects model (Higgins 2011c). However, a problem with the random‐effects model is that it assigns the same weight to all studies. Therefore, to test the robustness of our results, we will conduct a sensitivity analysis using the fixed‐effect model (Sensitivity analysis).

Where it is not possible to conduct a meta‐analysis, we will provide a narrative synthesis of the data.

'Summary of findings' tables

We will use GRADEpro 2015 to import data from Review Manager 2014 and create a 'Summary of findings' table for our main comparison: bisphosphonate versus placebo or no drug. We will include all of our primary and secondary outcomes (Types of outcome measures) in this table.

We will use the GRADE approach to assess the quality of the body of evidence (Guyatt 2008). For each outcome (Types of outcome measures), two independent review authors (from ZZ, EM, DM and CMD) will rate the quality of the evidence as high, moderate, low, or very‐low quality, according to the presence of the following factors:

  • limitations in the design and implementation of the studies, suggesting high likelihood of bias;

  • indirectness of evidence (indirect population, intervention, controls, outcomes);

  • inconsistency of results or unexplained heterogeneity;

  • imprecision of results (wide CIs), we will downgrade once if fewer than 400 participants for continuous data and fewer than 300 events for dichotomous data (Guyatt 2011); and

  • high probability of publication bias.

We will resolve any discrepancies by discussion.

Subgroup analysis and investigation of heterogeneity

Where sufficient data are present, we will perform the following subgroup analyses:

  • dosage of bisphosphonate, since response to treatment will vary with different dosages used;

  • duration of use, since response will vary with the duration of treatment;

  • monotherapy (bisphosphonate only) or multiple treatment (e.g. calcium and vitamin D or alfacalcidol);

  • participant age (e.g. preschool children (aged three to five years) versus school‐age children (aged five to 12 years)); and

  • classification of cerebral palsy according to motor ability, as assessed using the GMFCS.

If there are too few studies (less than three) per group, we will not conduct the particular subgroup analysis. 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 perform a sensitivity analysis to:

  • explore the impact of overall risk of bias on the results, by removing the results of studies deemed to be at high or unclear (or both) risk of bias;

  • explore the impact of missing data for our primary outcomes on the results, by comparing the results of studies with imputed data to studies with no imputed data; and

  • assess the influence of our choice of analysis model on the results from the meta‐analysis, by re‐analysing data using a fixed‐effect model instead of a random‐effects model.