Administración de bifosfonatos en niños con parálisis cerebral
Resumen
Antecedentes
La parálisis cerebral (PC) es un grupo heterogéneo de trastornos no progresivos de la postura o el movimiento, causados por una lesión del cerebro en desarrollo. La osteoporosis es frecuente en los niños con parálisis cerebral, sobre todo en los que tienen una motricidad gruesa reducida, y conlleva un mayor riesgo de fracturas. La motricidad gruesa de los niños con parálisis cerebral se puede clasificar mediante una herramienta denominada Gross Motor Function Classification System (GMFCS). Los bifosfonatos aumentan la densidad mineral ósea (DMO) y reducen las tasas de fractura. Los bifosfonatos se utilizan ampliamente en el tratamiento de la osteoporosis en adultos. Sin embargo, el uso de bifosfonatos en niños con PC sigue siendo controvertido, debido a la escasez de evidencia y a la falta de ensayos recientes que examinen la eficacia y la seguridad del uso de los bifosfonatos en esta población.
Objetivos
Examinar la eficacia y la seguridad del tratamiento con bifosfonatos en la DMO baja o la osteoporosis secundaria (o ambas) en niños con parálisis cerebral (niveles III a V del GMFCS) menores de 18 años.
Métodos de búsqueda
En septiembre de 2020 se realizaron búsquedas de estudios relevantes en CENTRAL, MEDLINE, Embase, otras seis bases de datos y dos registros de ensayos. También se buscó en las listas de referencias de revisiones sistemáticas, ensayos y estudios de casos relevantes identificados por la búsqueda, y se estableció contacto con los autores de los estudios relevantes en un intento por identificar literatura no publicada.
Criterios de selección
Todos los ensayos controlados aleatorizados (ECA) y cuasialeatorizados relevantes que compararan al menos un bifosfonato (administrado en cualquier dosis, por vía oral o intravenosa) con placebo o ningún fármaco, para el tratamiento de la DMO baja o la osteoporosis en niños de hasta 18 años con parálisis cerebral (niveles III a V del GMFCS).
Obtención y análisis de los datos
Se utilizaron los procedimientos metodológicos estándares previstos por Cochrane. No fue posible realizar metanálisis debido a que los datos no fueron suficientes, por lo que se proporciona una evaluación narrativa de los resultados.
Resultados principales
Se encontraron dos ECA relevantes (34 participantes). Ambos estudios incluyeron participantes con parálisis cerebral no deambulante o con parálisis cerebral y osteoporosis. Los participantes de ambos estudios eran similares en cuanto a la gravedad de la PC, la distribución etaria y el sexo. Los dos ensayos utilizaron diferentes bifosfonatos y diferentes duraciones de la intervención, pero no fue posible realizar una comparación en más detalle de las intervenciones debido a la falta de datos publicados de un ensayo.
Un ensayo recibió financiación y apoyo de fundaciones de investigación, académicas y hospitalarias, y las empresas farmacéuticas proporcionaron los componentes del suplemento de calcio y vitaminas; el otro ensayo no informó sobre las fuentes de financiación. Uno de los estudios se consideró con alto riesgo de sesgo y el otro con riesgo de sesgo incierto.
Desenlace principal. En comparación con placebo o ningún tratamiento, ambos estudios aportaron evidencia de certeza muy baja de una mejoría de la DMO al menos cuatro meses después de la intervención en los niños tratados con bifosfonato. Sólo un estudio (12 participantes) proporcionó detalles suficientes para evaluar una medida del efecto, e informó una mejoría a los seis meses después de la intervención en la puntuación z de la columna lumbar (diferencia de medias [DM] 18%; intervalo de confianza [IC] del 95%: 6,57 a 29,43; evidencia de certeza muy baja).
Desenlaces secundarios. Evidencia de certeza muy baja de un estudio encontró que los bifosfonatos redujeron los N‐telopéptidos (NTX) séricos más que el placebo; el otro estudio informó que tanto el bifosfonato más alfacalcidol como el alfacalcidol solo redujeron los NTX, pero no comparó los grupos.
Un estudio informó resultados no concluyentes entre los grupos para la fosfatasa alcalina específica del hueso (BAP) en suero. El otro estudio informó que tanto el bifosfonato más alfacalcidol como el alfacalcidol solo redujeron la BAP, pero no comparó los grupos.
Ninguno de los estudios aportó datos sobre el efecto del tratamiento con bifosfonatos sobre los cambios de la DMO volumétrica en el radio distal o la tibia, los cambios en la frecuencia de las fracturas, el dolor óseo o la calidad de vida. Un estudio informó que dos participantes tuvieron eventos febriles detectados durante su primera administración de la pauta posológica, pero no se informaron más eventos adversos en ninguno de los estudios relevantes.
Conclusiones de los autores
Según la evidencia disponible, hay evidencia de certeza muy baja de que el tratamiento con bifosfonatos podría mejorar la salud ósea de los niños con parálisis cerebral. Sólo fue posible incluir un estudio con 14 participantes en la evaluación del tamaño del efecto; por lo tanto, la precisión de la estimación del efecto es baja. Sólo fue posible evaluar un desenlace principal programado, ya que no se informaron suficientes detalles en los estudios relevantes.
Se requieren más investigaciones de ECA sobre el efecto y la seguridad de los bifosfonatos para mejorar la salud ósea en los niños con parálisis cerebral. Estos estudios deberían aclarar cuál es el tratamiento estándar óptimo con respecto a los ejercicios de carga y la administración de suplementos de vitamina D y de calcio, y deberían incluir la frecuencia de fracturas como un desenlace principal.
PICO
Resumen en términos sencillos
Tratamiento con bifosfonatos para mejorar la salud ósea de los niños con parálisis cerebral
¿Por qué es importante esta revisión?
La poca fuerza de los huesos es frecuente en las personas con parálisis cerebral (PC). Entre las causas se encuentran: la reducción de las actividades de carga que fortalecen los huesos, como caminar o correr, especialmente entre las personas que necesitan dispositivos de ayuda para la movilidad; la reducción de la ingesta de vitaminas y minerales que aumentan la fortaleza de los huesos, como el calcio y la vitamina D; y el aumento del uso de medicamentos que impiden la formación de huesos, como los anticonvulsivos. Esto conlleva un alto riesgo de fracturas óseas, incluso en caso de traumatismos muy leves. Los niños con parálisis cerebral que no pueden caminar corren un riesgo especialmente alto de tener una escasa resistencia ósea y fracturas en los huesos de las piernas. Los bifosfonatos son un grupo de medicamentos que se utilizan para mejorar la resistencia de los huesos. Los bifosfonatos se utilizan habitualmente en adultos con poca fuerza ósea. Sin embargo, se carece de evidencia para su uso en niños.
¿Qué preguntas pretende contestar esta revisión?
En primer lugar, ¿cuál es el efecto del tratamiento con bifosfonatos en comparación con el placebo (píldora falsa) o ningún tratamiento en diferentes medidas de resistencia ósea en niños de hasta 18 años con parálisis cerebral? Las medidas incluyen marcadores en sangre de la salud ósea, frecuencia de fracturas, dolor en los huesos y calidad de vida.
En segundo lugar, ¿hay efectos secundarios negativos?
¿Qué estudios se incluyeron en la revisión?
Se examinó la evidencia disponible para el uso del tratamiento con bifosfonatos en niños con PC hasta septiembre de 2020. Se encontraron dos ensayos que compararon el uso del tratamiento con bifosfonatos con placebo o ningún tratamiento para mejorar la resistencia ósea en niños con PC. Estos dos ensayos incluyeron un total de 34 participantes con parálisis cerebral de niveles de gravedad similares. Los participantes de ambos estudios tenían 16 años o menos, y había el mismo número de niños y niñas en cada ensayo. En ambos ensayos participaron niños que no podían caminar. Los dos ensayos utilizaron diferentes tipos de tratamientos con bifosfonatos, administrados durante seis meses en un estudio y 12 meses en el otro. No fue posible realizar una comparación adicional de estos tratamientos debido a la falta de información publicada en un ensayo.
Uno de los ensayos contó con el apoyo de fundaciones de investigación, académicas y hospitalarias, y las empresas farmacéuticas donaron componentes de los suplementos de calcio y vitaminas. El otro estudio no informó sus fuentes de financiación.
¿Qué revela la evidencia de la revisión?
Los resultados de ambos ensayos aportan alguna evidencia de que la administración de un tratamiento con bifosfonatos a los niños con parálisis cerebral durante al menos seis meses podría mejorar su resistencia ósea. La fuerza de este efecto sólo se pudo medir en un ensayo con 12 participantes. Esto indicó una mejoría media de la resistencia ósea del 18%, medida por la densidad mineral ósea (DMO). Sin embargo, debido al escaso número de participantes en ambos ensayos, a la gran variación de los resultados y a algunos problemas con la forma en que se realizaron los ensayos, esta conclusión es no está clara.
Cada estudio informó los resultados de los cambios en los marcadores en sangre de la resistencia ósea de forma diferente, lo que significa que no se cuenta con evidencia concluyente y no se puede establecer conclusiones sobre los efectos del tratamiento con bifosfonatos.
Ninguno de los ensayos informó sobre riesgos significativos o desenlaces adversos graves entre los niños sometidos al tratamiento con bifosfonatos.
Ningún ensayo examinó la cuestión de si el tratamiento con bifosfonatos tenía un efecto sobre los cambios en la densidad ósea real, ni la tasa de fracturas de los niños con PC.
Conclusiones de los autores
Se tiene una confianza limitada con respecto a si el tratamiento con bifosfonatos podría mejorar la salud ósea en los niños con PC.
Se necesitan más estudios para evaluar el efecto beneficioso y los riesgos del tratamiento con bifosfonatos en niños con PC. Los futuros estudios sobre los bifosfonatos deberían examinar los efectos de los bifosfonatos combinados con otras nuevas opciones de tratamiento.
Authors' conclusions
Summary of findings
| Bisphosphonate treatment (oral or intravenous) compared to placebo or no treatment for children under the age of 18 with cerebral palsy (GMFCS levels III to V) | ||||||
|---|---|---|---|---|---|---|
| Patient or population: children under the age of 18 with cerebral palsy (GMFCS levels III to V) | ||||||
| Outcomes | Anticipated absolute effects* (95% CI) | Relative effect | № of participants (Studies) | Certainty of the evidence | Comments | |
| Risk with placebo or no treatment | Risk with bisphosphonate treatment (oral or intravenous) | |||||
| Change in BMD lumbar spine (%, assessed at 6 months post‐intervention) | The mean % change in BMD lumbar spine was 15% (SE ± 5%) | The mean % change in BMD lumbar spine was 18% larger in the intervention group | ‐ | 12 | ⊕⊝⊝⊝ | ‐ |
| Change in volumetric BMD of distal radius or tibia | ‐ | ‐ | ‐ | (0 studies) | ‐ | Not measured in any trial |
| Change in fracture frequency | ‐ | ‐ | ‐ | (0 studies) | ‐ | Not measured in any trial |
| Adverse events (ongoing reporting, up to 6 months post‐intervention) | 2 of 6 participants receiving their 1st 3‐day pamidronate dosing session had elevated axillary temperature (> 37 °C), but not during any subsequent dosing session. Participants receiving placebo treatment recorded no elevation in body temperature during the 1st dosing session but was noted in 4 subsequent sessions. No differences in white blood cell count were noted between treatment groups. No other adverse events were reported. | 12 | ‐ | ‐ | ||
| Change in NTX (assessed 4 to 6 months post‐intervention) | One study reported that bisphosphonate reduced serum NTX more than placebo; the other study reported that both bisphosphonate and no treatment reduced NTX (r = 0.89, P < 0.001 versus r = 0.69, P = 0.003), but did not compare groups. | 32 | ⊕⊝⊝⊝ | ‐ | ||
| Change in BAP (assessed 4 to 6 months post‐intervention) | One study reported inconclusive results between groups for BAP. The other study reported that both bisphosphonate and no treatment reduced BAP (r = 0.89, P = 0.02 versus r = 0.72, P = < 0.001), but did not compare groups. | 32 | ⊕⊝⊝⊝ | ‐ | ||
| *The risk in the intervention group (and its 95% CI) is based on the risk in the placebo or no treatment group and the relative effect of the intervention (and its 95% CI). BAP: bone‐specific alkaline phosphatase; BMD: bone mineral density; CI: confidence interval; GMFCS: Gross Motor Function Classification System; MD: mean difference; NTX: N‐telopeptides; RCT: randomised controlled trial; SE: standard error | ||||||
| GRADE Working Group grades of evidence | ||||||
| aCertainty of evidence was downgraded by two levels, one study was at high risk of bias and one study was at unclear risk of bias. | ||||||
Background
Cerebral palsy is a heterogeneous group of non‐progressive disorders of posture or movement, due to an injury or lesion of the developing brain. Cerebral palsy is the most common form of childhood disability, with worldwide incidence rates between 1.5 and 4 per 1000 live births (Pharoah 1998; Reddihough 2003; Stanley 2008; Stavsky 2017). The prevalence of moderate to severe cerebral palsy in Europe, defined by the Gross Motor Function Classification System (GMFCS) Levels III to V, indicating a range of a child's ability to walk, from walking using a hand‐held mobility device to children who are transported using a mobility device in all settings, or an intellectual quotient less than 50, is approximately 0.78 per 1000 live births (Sellier 2016).
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). Several factors increase the risk of osteoporosis in children with cerebral palsy, including reduced weight‐bearing activities that improve bone mineral density (BMD), nutritional deficiencies of calcium and vitamin D, decreased sun exposure, and increased exposure to medications that cause low BMD, including anti‐epileptic drugs and glucocorticoids (Ko 2020). The prevalence of low BMD in children with severe cerebral palsy is 77% (95% confidence interval (CI) 65.0% to 87.1%) and the annual incidence rate of fractures is 4% (Mergler 2009). A longitudinal assessment of changes in bone density in adolescents with cerebral palsy reported an annual increase in areal BMD (aBMD) of 4% to 8%, similar to that in typically developing children (Trinh 2019). This finding is also reflected in the stability of the z‐score in children with cerebral palsy over time. This was a retrospective study of young people with cerebral palsy at risk of low BMD, all of whom had a z‐score less than −2 at the time of first assessment, at a mean age of 13.9 (± 3.1) years. This suggests that the deficit in bone mass is accrued during the first decade of life, so earlier interventions may be of greatest benefit. Many of those who sustain a fracture will sustain repeated fractures (Henderson 2002; Mergler 2009). The most common site of fracture is the distal femur (Fehlings 2012). Prevalence of femur fractures has been variably estimated at 14% in children with severe cerebral palsy (Uddenfeldt 2013). The incidence of fracture in children with severe cerebral palsy has been reported to be from 7% to 9.7% per year (Stevenson 2006). Severe cerebral palsy is defined as Level IV or V, according to the 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 the use of anticonvulsants. Bone mineralisation is also adversely affected by the use of anticonvulsants (Henderson 2002). The most commonly used method to assess 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; Anonymous 2013).
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, and thus additional, large randomised controlled trials (RCTs) are needed (Hough 2010).
Description of the intervention
Bisphosphonate increases BMD, and reduces fracture rates by inactivating osteoclasts (large multinucleated cells that degrade or reabsorb bone), which are responsible for the breakdown of existing bone cells. Bisphosphonate is used widely in the treatment of adult osteoporosis, but its use in children is controversial, because of a lack of long‐term safety and efficacy data (Allington 2005; Boyce 2014; Simm 2018).
It should be noted that the primary defect of bones 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 remains 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 an increased incidence of atypical femoral fractures (Shane 2013). It is unclear whether there are significant risks of adverse effects from long‐term use of bisphosphonate in children. A retrospective review of eight children with spinal muscular atrophy and low BMD, who received bisphosphonate therapy for over one year, reported an atypical femoral fracture in one child (Nasomyont 2020). A case report identified a child with idiopathic juvenile arthritis and low BMD, who received bisphosphonate treatment for two years, and developed an atypical femoral fracture (Boyce 2017). Outside of these two small studies, it is unclear if long‐term bisphosphonate treatment conveys a significant risk of atypical femoral fractures in this population. Osteonecrosis of the jaw has also been linked with long‐term bisphosphonate use in adults, but not in children, 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 randomised controlled trials (RCT) that provided evidence that bisphosphonate improved BMD, reduced fracture risk, and improved pain in children with OI.
How the intervention might work
Bisphosphonates are a synthetic analogue of pyrophosphate, an endogenous regulator of bone metabolism. They increase BMD by inhibiting osteoclast activity or by inducing osteoclast apoptosis (Ukon 2019). Bisphosphonate can be administered via the oral or intravenous (IV) route, but as oromotor dysfunction, or gastrointestinal reflux (or both) are often associated with cerebral palsy, oral 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 oral 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, and arthritis (Russell 2011). A recent retrospective review of bisphosphonate treatment to prevent recurrent fractures in 32 children with cerebral palsy reported a post‐treatment reduction in fracture frequency from 2.4 fractures per year to 0.1 fractures per year, with an average follow‐up time of 6.4 years (Sees 2016). Only 11 children (34%) sustained a fracture post‐treatment.
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, osteogenesis imperfecta. However, more recent guidelines often recommend the use of pamidronate for children under two years old, with OI, before switching to zoledronate in older children (Simm 2018). A recent retrospective review on the use of zoledronic acid (ZA) for 81 young people under 21 years old, with bone disorders, reported that ZA‐related adverse events were common, particularly after the first infusion and in bisphosphonate‐naive people, but were typically mild and easily managed (George 2015). 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 an 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 remains 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 (Simm 2018). 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 bone mineral density or secondary osteoporosis (or both) in children with cerebral palsy (Gross Motor Function Classification System 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 bone mineral density (BMD) or secondary osteoporosis (or both) in children and adolescents with cerebral palsy.
Types of participants
Children under 18 years of age with cerebral palsy (Gross Motor Function Classification System (GMFCS) Levels III to V).
We did not include data from studies that did 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 intravenous (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
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Change in areal BMD z‐score of the lumbar spine, total body minus the head, or lateral distal femur, measured by dual X‐ray absorptiometry (DXA scan)
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Volumetric BMD of distal tibia or radius, using peripheral, quantitative computerised tomography (pQCT)
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Fracture frequency: number of incident fractures (clinical, radiographic, or both) noted per participant per year before and after bisphosphonate treatment
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Adverse effects associated with bisphosphonate use, experienced by the participants (which could have included 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
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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 was impacted or overly suppressed
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Bone pain and quality of life, as reported by the participant or the child’s parents, before and after bisphosphonate use
We included studies that used any validated scale to measure the primary and secondary outcomes listed above.
Both included studies assessed outcomes between four and six months post‐intervention.
We included all of our outcomes in a summary of findings table.
Search methods for identification of studies
We searched the following databases, using the search strategies in Appendix 2. We did not apply a study methods filter, or limit the searches by language, date, or publication status.
Electronic searches
We searched the following electronic databases and trial registers for all available years, up to September 2020.
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Cochrane Central Register of Controlled Trials (CENTRAL; 2020, Issue 8) in the Cochrane Library, which includes the Cochrane Developmental, Psychosocial and Learning Problems Group Specialised Register (searched 6 September 2020);
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MEDLINE Ovid (1946 to 6 September 2020);
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MEDLINE In‐Process and Other Non‐Indexed Citations Ovid (6 September 2020);
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MEDLINE Epub ahead of Print Ovid (6 September 2020);
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Embase Ovid (1974 to 2017 week 35);
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Embase.com Elsevier (2017 to 6 September 2020);
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CINAHL Plus EBSCOhost (Cumulative Index to Nursing and Allied Health Literature; 1937 to 6 September 2020);
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Cochrane Database of Systematic Reviews (CDSR; 2020, Issue 8), in the Cochrane Library (searched 6 September 2020);
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Database of Abstracts of Reviews of Effects (DARE; 2015, Issue 2; final issue) part of the Cochrane Library (searched 30 August 2017);
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Epistemonikos (www.epistemonikos.org; searched 6 September 2020);
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Science Citation Index and Social Sciences Citation Index Web of Science (SCI and SSCI; 1970 to 6 September 2020);
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Clinicaltrials.gov (clinicaltrials.gov; searched 6 September 2020);
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World Health Organization International Clinical Trials Registry Platform (WHO ICTRP; apps.who.int/trialsearch; searched 6 September 2020).
Searching other resources
We searched the reference lists of relevant systematic reviews, trials, and case studies identified by the search. We contacted the authors of relevant studies in an attempt to identify unpublished literature.
Data collection and analysis
In the following section, we report only the methods used in the review. Planned and unused methods can be found in Table 1 and the review Protocol (Zareen 2017).
| Section of Protocol (Zareen 2017 ) | Planned approach | Why the methods were not used |
|---|---|---|
| Types of outcome measures | We had planned to 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). | There were insufficient data from the studies identified to complete this analysis. |
| Assessment of risk of bias in included studies | We used the Cochrane RoB 1 tool when assessing the risk of bias in each domain for both included studies. Neither study was assessed as having an unclear risk of bias in all domains. In future updates of this review, we will apply the Cochrane RoB 2 tool in assessing the risk of bias for each domain in included studies, and apply the risk of bias due to missing evidence tool in assessing the risk of non‐reported evidence once the final version is released. | The review was conducted prior to the publication of updated guidelines on the assessment of risk of bias in included studies. |
| Measures of treatment effect | Dichotomous data We had intended to calculate the effect size as a risk ratio, and present it with 95% confidence intervals (CI). We had planned to consider a change as an improvement in bone mineral density (BMD) of the femur (lateral or distal), lumbar spine, and total body minus the head, measured by dual‐Energy x‐Ray absorptiometry (DXA), or volumetric BMD, measured by peripheral, quantitative computerised tomography (pQCT). | The study did not identify any relevant dichotomous data. |
| Continuous data For studies that measured the same outcome using different scales, we had planned to use the standardised mean difference (SMD) with 95% CI. | The studies used the same measures to assess the outcomes. | |
| Multiple outcomes Had studies provided multiple, interchangeable measures of the same construct at the same point in time, we would have calculated the average SMD across the outcomes and the average estimated variances (Borenstein 2009). The aim here would have been to prevent studies that reported on more outcome measures from receiving more weight in an analysis than studies that reported on only a single outcome measure. The effect estimate could have been presented as a mean difference, by transforming the SMD effect estimate backwards to one of the well‐known scales, together with a pre‐defined minimal clinically important difference. | No studies measuring multiple outcomes were identified in this review. | |
| Unit of analysis | Cluster‐randomised trials Had we identified cluster‐randomised trials, we would have sought direct estimates of the effect from an analysis that accounted for the cluster design. If the analysis had not accounted for the cluster design in the cluster trial, we would have used the approximately correct analysis approach, as presented in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2020a). | We did not identify any cluster‐randomised trials in this review. |
| Cross‐over trials We had only planned to include cross‐over trials in the meta‐analysis when the data were clear of carry‐over effects. We would have combined the results of cross‐over studies with those of parallel studies by imputing the correlation coefficient from an included study that presented individual participant data, and used this to calculate the standard deviation (SD). We would have used the generic inverse‐variance method to conduct a meta‐analysis of this data (Higgins 2020a). To avoid presenting repeated measurements reported in a study, we would have only included data from one time point from an individual study in any single meta‐analysis. | We did not identify any cross‐over trials in this review. | |
| Studies with multiple treatment groups Had we identified any studies with multiple treatment groups, we would have combined all relevant intervention groups and compared them with all relevant control groups, making single pair‐wise comparisons. If this approach had not allowed for investigation of intervention‐related sources of heterogeneity, we would have included 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 would have added the number of participants with intervention and the total number of participants, across the groups (Higgins 2020a). In case of continuous outcomes, we would have combined the mean and standard deviation using the formulae described in Chapter 10 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2020). | We did not identify any studies with multiple treatment groups. All relevant studies were a direct comparison of treatment groups to placebo or standard treatment. | |
| Dealing with missing data | If additional data had been made available, we had planned to include them in the analysis. If we received no response from the study authors, or the data were not made available, we had planned to:
We also would have specified the methods used to estimate the data in the 'Characteristics of included studies' tables and performed a Sensitivity analysis to compare the results of analyses with imputed missing data to those without imputed missing data. | It was not possible to impute missing data in the review. |
| Assessment of heterogeneity | We had planned to assess statistical heterogeneity between studies by visual inspection of the forest plot for overlapping CI, using the Chi²test 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 would have judged I² values based on the thresholds listed below, as suggested in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2020):
These thresholds can be misleading. Therefore, when considering the importance of I², we would have taken 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. Also, we would have estimated and presented Tau², along with its CI to provide an estimate of the amount of between‐study variation. | We did not assess statistical heterogeneity in this review as there were insufficient data to conduct a meta‐analysis. |
| Assessment of reporting bias | Had data from a sufficient number of studies been available (at least 10 studies in a meta‐analysis), we would have drawn funnel plots and tested for funnel plot asymmetry (Egger 1997). If we had found any asymmetry of the funnel plot, we would have looked for possible causes (such as publication bias or true heterogeneity) that we might have considered to have a likely influence on the observed effect sizes in our interpretation of the results. However, given that common tests of publication bias lack sensitivity, we would have considered the possible influence that a dominance of small trials might have had on pooled effect sizes in our interpretation, where indicated. | We could not assess reporting bias by drawing funnel plots and testing for funnel plot asymmetry due to an insufficient number of included studies. |
| Data synthesis | If sufficient data had been included, we would have conducted a meta‐analysis. As we would have expected some heterogeneity in intervention characteristics, we would have pooled the available data using the random‐effects model (Deeks 2020). 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 would have conducted a sensitivity analysis using the fixed‐effect model. | We could not complete a meta‐analysis due to insufficient data and so provided a narrative description of the results instead. |
| Subgroup analysis and investigation of heterogeneity | We had planned to perform the following subgroup analyses:
| There were insufficient data to conduct subgroup analyses. |
| Sensitivity analysis | We had planned to perform a sensitivity analysis if there were sufficient data (10 or more studies). Our plan was to:
| We did not perform a sensitivity analysis due to an insufficient number of included studies. |
Selection of studies
Two review authors (TH and PS) independently checked the titles and abstracts of all records yielded by the search, and excluded those that did not meet the inclusion criteria outlined earlier. In cases that appeared to meet the inclusion criteria, or when there was any doubt as to whether the record should be excluded, both review authors retrieved the full text of the report and independently assessed it for eligibility. They resolved any disagreements by discussion, or if necessary, by consulting a third review author (EM). We recorded our decisions in a PRISMA diagram (Moher 2009).
Data extraction and management
We used a data extraction form to ensure standardisation of the data extracted. The form was piloted by TH and PS prior to use.
Two review authors (TH and PS) independently extracted the following data, using the standardised form developed for this purpose:
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study design;
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sample size: treatment and control groups;
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study population (treatment and control groups): sex, age, ambulatory, or nonambulatory cerebral palsy gross motor function (GMFCS Level), and any previous fracture;
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intervention: type of intervention, bisphosphonate orally or IV, dosage and duration of treatment, monotherapy or multiple treatment (e.g. calcium and vitamin D or alfacalcidol);
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outcome measures: improvement in BMD, fracture rate, adverse effects, changes in serum or urine bone markers, bone pain, and quality of life;
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potential conflicts of interest; and
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stated or declared conflicts of interest.
Both review authors resolved disagreements regarding the extraction of data by discussion.
We conducted the data analyses using Review Manager 5 (RevMan 5) software (Review Manager 2020).
Assessment of risk of bias in included studies
Using Cochrane’s risk of bias tool (RoB 1 (Higgins 2011a)), two review authors (TH and PS) independently assessed each study for risk of bias across the following domains.
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Random sequence generation: was the allocation sequence adequately generated?
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Allocation concealment: was allocation adequately concealed?
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Blinding of participants and personnel: was knowledge of the allocated intervention adequately prevented during the study?
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Blinding of outcome assessment: was knowledge of the allocated intervention adequately prevented during the study?
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Incomplete outcome data: were incomplete outcome data adequately addressed?
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Selective reporting: are reports of the study free of suggestion of selective outcome reporting?
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Other sources of bias: was the study apparently free of other problems that could put it at a high risk of bias?
We assigned 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 discussed any disagreements until a consensus was reached. When we rated one or more domain(s) as being at high risk of bias, we judged the study to be at high risk of bias overall. We only rated a study as being at low risk of bias overall if we rated it as such for all domains. When a study included domains rated as unclear and low risk of bias, we judged the study to be at unclear risk of bias overall.
We present our judgements with reasons in the risk of bias tables.
Measures of treatment effect
Continuous data
For continuous data, where the same continuous outcome was measured using the same scale, we presented the effect size as a mean difference (MD) with 95% confidence intervals (CIs).
Unit of analysis issues
We did not encounter any unit of analysis issues.
Dealing with missing data
We identified and reported missing data (dropouts, withdrawals, missing summary data) in the Characteristics of included studies and risk of bias tables.
We requested missing data from the authors of the Iwasaki 2008 study, but did not receive a response. There were insufficient reported data to impute missing outcome data. We discussed this in the text, and conducted an available case analysis. We also discussed the possible impact of the missing data on the results in the discussion section.
Assessment of heterogeneity
We assessed clinical and methodological heterogeneity by comparing similarities and differences in the characteristics of the participants recruited to both included studies, study designs, and methodologies, including randomisation, intervention regimens, and outcome assessments performed in both studies. We did not assess statistical heterogeneity in this review as there were insufficient data to conduct a meta‐analysis.
Assessment of reporting biases
Neither study published a protocol prior to commencement of the trial. Therefore, we compared the reported measured outcomes in the methods section of each trial with the results reported. In addition, we were unable to draw funnel plots and test for funnel plot asymmetry, because there were too few included studies.
Data synthesis
We entered the data into Review Manager 2020. We could not complete a meta‐analysis due to insufficient data, and so provide a narrative description of the results instead.
Subgroup analysis and investigation of heterogeneity
There were insufficient data to conduct subgroup analyses, as there were too few studies (less than three) per group, and too few participants per study (the requirement for a sample size four times higher than that required for adequate power to detect an overall effect was not met).
Sensitivity analysis
We did not perform a sensitivity analysis due to insufficient included studies.
Summary of findings and assessment of the certainty of the evidence
We used GRADEpro GDT to import data from Review Manager 2020 and create a summary of findings table for our main comparison: bisphosphonate versus placebo or no drug. We included all of our primary and secondary outcomes (Types of outcome measures), measured at four to six months post‐intervention in this table.
We used the GRADE approach to assess the certainty of the body of evidence (Guyatt 2008). For each outcome, two independent review authors (TH and PS) rated the certainty of the evidence as high, moderate, low, or very low, according to the presence of the following factors:
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limitations in the design and implementation of the studies, suggesting high likelihood of bias;
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indirectness of evidence (indirect population, intervention, controls, outcomes);
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inconsistency of results or unexplained heterogeneity;
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imprecision of results (wide CIs); we downgraded once if there were fewer than 400 participants for continuous data, or fewer than 300 events for dichotomous data (Guyatt 2011); and
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high probability of publication bias.
We resolved any discrepancies by discussion.
Results
Description of studies
Results of the search
Our original literature search identified 305 records; the top‐up search in September 2020 identified a further 109 records. Following the exclusion of duplicates, 376 records remained. We identified no further studies through a search of the grey literature, and did not identify any ongoing studies from our searches of clinical trial registers. We excluded 345 records during title and abstract screening, leaving 31 records for which we retrieved the full texts for further examination. From these, we excluded 22 studies (from 24 reports) due to ineligible study designs, and five studies (from five reports) due to ineligible populations. Of the two studies that met the eligibility criteria, one study did not provide an adequate description of the results, and our requests for further information to the study author were not returned. See Figure 1.
Study flow diagram
Included studies
We included two studies (34 participants) in this review (Henderson 2002; Iwasaki 2008). See Characteristics of included studies for details.
Study design
Both included studies were double‐blind randomised controlled trials (RCT), designed to assess the efficacy and safety of bisphosphonate use in children with cerebral palsy. One study was placebo‐controlled (Henderson 2002).
Participants
Both studies recruited young people with cerebral palsy, up to the age of 16 years.
Henderson 2002 recruited 14 nonambulatory children and adolescents with quadriplegic cerebral palsy. Participants were matched for age (range = 6 to 16 years, mean difference = 2.4 months), sex (six pairs matched, one pair unmatched), and race (13 participants were white). All participants had an age‐normalised bone mineral density (BMD) z‐score of ≤ 2.0. One pair of children withdrew from the study and were not included in the analyses.
Iwasaki 2008 recruited 20 young people with cerebral palsy and secondary osteoporosis. The participants included 10 boys; the age range was 1 year to 16 years (mean = 7.6 years).
Settings
Both studies were conducted in hospital environments; one in Japan and one in the USA.
Interventions
Both studies assessed the efficacy of bisphosphonate treatment compared to control groups on post‐intervention changes in BMD z‐scores.
Henderson 2002 used pairwise randomisation to assign half of the sample to the bisphosphonate treatment group and half to the control group. Participants were recruited as pairs matched for age, sex, and race. They received intravenous pamidronate, a second generation bisphosphonate, daily for three consecutive days. This three‐day dosing session was repeated at three‐month intervals for one year (five dosing sessions, 15 total doses); they were assessed at six months post‐intervention. Each daily dose was 1 mg pamidronate/kg body weight, but not < 15 mg or > 30 mg. Participants in the intervention group also received vitamin D supplementation.
Iwasaki 2008 specified the use of oral risedronate, a third generation bisphosphonate. The drug was given to one group of participants for six months; they were assessed at four months post‐intervention; no further details regarding dosage, or frequency or method of administration were provided. All participants in the treatment group were also treated with alfacalcidol (reported as alfacarcidol but understood internationally as alfacalcidol) during the trial.
Controls/Comparators
Henderson 2002 compared bisphosphonate efficacy to placebo treatment. All participants in the study, regardless of treatment group, were treated with a daily supplement over the 18‐month study period. The supplement contained 1000 mg of calcium (10 mL calcium carbonate), a paediatric multivitamin, and additional vitamin D (400 IU of calciferol).
Iwasaki 2008 compared the outcomes of participants treated with risedronate (plus alfacalcidol) to participants with no treatment (alfacalcidol alone).
Outcomes
Primary outcomes
One of the studies measured and reported the primary outcome (post‐intervention change in BMD z‐score of the lumbar spine, total body minus the head, or lateral distal femur (Henderson 2002)). Post‐intervention BMD z‐scores were measured at six months following completion of the intervention. Iwasaki 2008 measured the primary outcome and presented results graphically; however, they only reported the results of significant tests of between‐groups differences in change in BMD, without any measure of the effect size. Therefore, we could not include the results in a quantitative analysis.
Neither study reported changes in fracture frequency or improvement in volumetric BMD of distal tibia or radius, using peripheral, quantitative computerised tomography (pQCT) following intervention completion.
Henderson 2002 also reported febrile response in participants treated with bisphosphonate, but no other adverse effects were noted.
Secondary outcomes
Both studies measured and reported post‐intervention changes in serum bone markers, bone‐specific alkaline phosphatase, and N‐telopeptides.
Neither study reported outcomes for changes in bone pain or quality of life following intervention completion.
Funding
The Henderson 2002 study was supported by Roxane Laboratories Inc, Meade Johnson, and Schwarz Pharma, which donated the various components of the calcium plus vitamin supplement; however, there was no discussion of support or supply of bisphosphonate therapy. The trial was also supported by a grant from the United Cerebral Palsy Research and Educational Foundation; at the University of North Carolina, by the General Clinical Research Centers program of the Division of Research Resources; National Institutes of Health (grant RR00046); a career award from the National Institute of Arthritis, Musculoskeletal, and Skin Diseases (AR02132); and the duPont Hospital for Children by the Nemours Foundation (W20‐8930).
Iwasaki 2008 did not state the source of funding for their trial.
Excluded studies
We excluded 27 studies (29 full‐text reports); for details, see the Characteristics of excluded studies tables. We excluded 22 studies due to ineligible study designs for this review, and five RCTs due to ineligible populations.
Risk of bias in included studies
We assessed the risk of bias in both studies using the Cochrane RoB 1 tool (Higgins 2011a; Higgins 2011b). We judged one study to have an overall high risk of bias, due to significant differences in baseline demographics between the groups without further exploration of this issue, and insufficient information reported to allow us to complete a full assessment of the methodology used, leading us to judge some elements as unclear risk of bias, and others as high risk of bias (Iwasaki 2008). The second study included several domains that we judged as unclear risk of bias, due to insufficient details reported about the study methodology; overall, we judged the study to have an unclear risk of bias Henderson 2002.
We summarise our judgements below, and graphically in Figure 2 and Figure 3. A full account of our assessment can be found in the risk of bias tables, included with the Characteristics of included studies tables.
Risk of bias summary: review authors' judgements about each risk of bias item for each included study
Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies
Allocation
Sequence generation
We rated Henderson 2002 at unclear risk of bias as there was insufficient detail provided regarding the randomisation process. We judged Iwasaki 2008 at high risk of bias due to inadequate discussion of the methodology used, and significant pre‐treatment differences in the primary outcome measure (BMD), with no further exploration of these differences.
Allocation concealment
We rated both studies at unclear risk of bias, as neither study provided adequate detail to fully assess the procedures used to maintain concealment of the allocation group from study personnel.
Blinding
Blinding of participants and personnel
We rated both studies at unclear risk of performance bias, as neither study provided adequate detail to fully assess the procedures used for blinding participants and personnel.
Blinding of outcome assessment
We rated both studies as unclear risk of detection bias, as neither study provided adequate detail to fully assess the procedures used for blinding outcome assessors.
Incomplete outcome data
We rated both studies at low risk of attrition bias, as there were low attrition rates in both studies. In the Henderson 2002 study, one of seven pairs of participants withdrew from the study. Both participants in the pair withdrew, the groups were matched, and the reason for withdrawal, participant time commitment, was explained in the study. Results were available for all participants in the Iwasaki 2008 study.
Selective reporting
We could not assess a priori methods as there were no available published protocols. Nonetheless, we rated both studies at low risk of reporting bias, as both studies appeared to have reported on all outcomes stated in the methods sections of the reports.
Other potential sources of bias
We did not identify any other sources of potential bias in either study, and so we rated both at low risk of other bias.
Effects of interventions
See summary of findings Table 1.
Unfortunately, as the two studies identified did not report results in sufficient detail and in a similar manner, we were unable to combine the results in a meta‐analysis; therefore, we can only report the individual study results.
Bisphosphonate treatment (oral or intravenous) versus placebo or no treatment
Primary outcomes
Change in BMD z‐score of the lumbar spine, total body minus the head, or lateral distal femur
Both studies measured the post‐intervention change in BMD z‐score: Henderson 2002 at six months, and Iwasaki 2008 at four months.
Henderson 2002 measured BMD z‐score in multiple anatomical locations in participants treated with bisphosphonate (N = 6), and in participants in the placebo group (N = 6). Compared to participants in the placebo group, those treated with bisphosphonate had a improved BMD z‐score in the lumbar spine (MD 18%, 95% CI 13.33 to 22.67; very low certainty evidence; Analysis 1.1); metaphysis of the distal femur just proximal to the growth plate (region one; MD 80%, 95% CI 62.52 to 97.48; very low certainty evidence; Analysis 1.2); region of transition between the broad metaphysis of the distal femur and the narrow femoral shaft (region two; MD 27%, 95% CI 19.62 to 34.38; very low certainty evidence; Analysis 1.3); and distal portion of the femoral diaphysis (region three; MD 12%, 95% CI 6.34 to 17.66; very low certainty evidence; Analysis 1.4).
Iwasaki 2008 measured changes in BMD between participants in the bisphosphonate group (N = 10; risedronate plus alfacalcidol), and participants in the no treatment group (N = 10; alfacalcidol alone). The study authors only provided results for significance tests, so we could not assess the magnitude of the effect size. They reported that treatment improved post‐intervention BMD in both groups (alfacalcidol alone: P = 0.003; bisphosphonate plus alfacalcidol: P = 0.003). However, the two groups are not comparable since the BMD was not similar at baseline between groups (P = 0.008). Accepting this limitation of the study, the results suggest that bisphosphonate plus alfacalcidol might improve BMD more than alfacalcidol alone (P = 0.02).
While both trials found that bisphosphonate treatment lead to a better improvement in BMD z‐scores in participants with cerebral palsy, we could not estimate the size of the pooled effect due to differences in reporting methods. We contacted the authors of the Iwasaki 2008 study for further statistical details, but did not receive a response.
Volumetric BMD
Neither study reported data on differences in changes in volumetric BMD following treatment intervention.
Fracture frequency
Neither study reported data on differences in changes in fracture frequency following treatment intervention.
Adverse effects
Henderson 2002 reported consistently elevated axillary temperature (> 37 °C) in two of six participants receiving their first three‐day pamidronate dosing session, but not during any subsequent dosing session. Participants receiving placebo treatment recorded no elevation in body temperature during the first dosing session, but was noted in four subsequent sessions. No differences in white blood cell count were noted between treatment groups. No other adverse events were reported.
Iwasaki 2008 did not report adverse events.
Secondary outcomes
Changes in serum or urine bone markers
Both studies measured post‐intervention changes in serum bone markers.
N‐telopeptides (NTX)
Henderson 2002 reported serum results graphically and descriptively but did not provide a numerical summary.
Iwasaki 2008 measured pre‐ and post‐intervention NTX levels and reported significant correlations between pre‐ and post‐intervention NTX/Creatinine levels in both the bisphosphonate (r = 0.89, P < 0.001) and no treatment groups (r = 0.69, P = 0.003). There was no discussion or presentation of differences in post‐intervention changes in NTX alone, or in differences between groups. However, Iwasaki 2008 reported there was no significant correlation between the post‐intervention change in NTX and the post‐intervention change in BMD.
Bone‐specific alkaline phosphatase (BAP)
Henderson 2002 reported no post‐intervention changes in BAP following treatment with pamidronate. There was no further discussion or presentation of results.
Iwasaki 2008 reported a post‐intervention reduction in BAP levels in both groups. They reported significant correlations between the pre‐ and post‐intervention BAP levels for both the bisphosphonate (r = 0.89, P = 0.02) and the no treatment groups (r = 0.72, P = < 0.001). There was no discussion or presentation of differences in post‐intervention changes in BAP between groups.
Osteocalcin
Henderson 2002 reported no post‐intervention change in osteocalcin following treatment with pamidronate. There was no further discussion or presentation of results.
Iwasaki 2008 did not report measurement or outcomes for osteocalcin.
Bone pain and quality of Life
Neither study reported data on either bone pain or quality of life following treatment.
Discussion
Summary of main results
We evaluated the evidence for bisphosphonate treatment to improve bone health in children with cerebral palsy and low bone mineral density (BMD) or osteoporosis.
We included two small studies (N = 34) that compared the effect of bisphosphonate treatment to control on bone health in children with cerebral palsy, under 16 years of age. Neither study reported data on changes in volumetric BMD, fracture frequency, bone pain, or quality of life. We were not able to combine the data from the studies in a meta‐analysis, due to differences in reporting methods.
There was very low certainty evidence from one study that, compared to placebo, bisphosphonate treatment improved BMD z‐scores at six months post‐intervention in the lumbar spine, in femur region one (metaphysis just proximal to the growth plate), and femur region two (region of transition between the broad metaphysis and narrow femoral shaft), but not in femur region three (distal portion of the femoral diaphysis).
The other study reported changes descriptively and graphically for BMD at four months post‐intervention for children treated with bisphosphonates and vitamin D (bisphosphonate group) compared to those treated with vitamin D alone (no treatment group). They described an improvement in BMD in both groups, with more improvement in the bisphosphonate group.
One study described febrile events in two children receiving bisphosphonates during their first dosing session, and subsequently on four occasions amongst children receiving placebo treatment. They did not note any differences in white blood cell counts or any other adverse events.
One study reported that bisphosphonate reduced serum N‐telopeptides (NTX) more than placebo, but the results were inconclusive between groups for bone‐specific alkaline phosphatase (BAP). The other study reported a reduction in NTX and BAP in both the bisphosphonate and no treatment groups, but did not compare the difference between groups.
Overall completeness and applicability of evidence
We included two small studies, with a total sample size of 34 participants that reported the effect of bisphosphonate treatment on post‐intervention changes in BMD. We were unable to combine results because of differences in comparators and unavailability of usable data.
Both studies were carried out over 10 years ago, and we identified no further completed studies of bisphosphonate treatment in children with cerebral palsy since then. In recent years, several other therapies to improve BMD in children with cerebral palsy have been investigated, including weight‐bearing activities and vitamin D supplementation, with or without calcium. The effect of bisphosphonate must now be assessed in the context of recent evidence of other interventions to improve osteoporosis and low BMD in children with cerebral palsy.
Both studies were completed in high‐resource countries (USA and Japan). The availability of complementary therapies and variation in treatments for children with cerebral palsy is likely to be different in low‐resource countries. This limits the generalisability of the results of this review to low‐resource settings.
While low BMD is an important risk factor for fractures in this population, neither study measured fracture frequency, bone pain, or quality of life. These are measures that are of great significance to children in this population, and limits the value of the results of the included studies.
We conclude that there is very low certainty evidence to suggest bisphosphonate treatment may improve BMD in children with cerebral palsy; however, we cannot estimate the size of this effect nor the impact this change in BMD may have on fracture frequency, bone pain, or quality of life in this group of children.
Quality of the evidence
The overall certainty of the evidence from this study is very low for each outcome presented in summary of findings Table 1. We identified only two studies, both with small participant numbers; one of which was at overall high risk of bias, and one at unclear risk of bias due to insufficient data reported.
We applied the GRADE approach to assess the certainty of the evidence for this review. We downgraded the certainty of evidence by three levels for two reasons: 1) downgraded by two levels due to study limitations, as we considered there to be substantial risk of bias; one study was at high risk of bias and one study was at unclear risk of bias and 2) downgraded by one level as it was not possible to assess the pooled effect size of the two studies due to reporting differences and very serious imprecision, with very wide confidence intervals reflecting the small sample sizes; in some cases, the evidence was based only on one RCT of 12 participants.
Potential biases in the review process
For this review, we followed the criteria and methodology outlined in the Methods section, in which we adhered to standard methodological procedures expected by Cochrane. We minimised risk of bias in the review by employing two independent authors to screen records and reports, extract data, and assess the certainty of the evidence from all studies identified by the search and deemed relevant for inclusion. The search strategy is outlined in Appendix 2; no restrictions by language or publication type were applied. The number of records yielded by the search strategy was low, so we made significant efforts to identify other relevant studies through discussion with key experts and by conducting searches of the grey literature. We did not identify any additional studies eligible for inclusion and other, recent systematic reviews have not included any other studies suitable for our review. However, the possibility remains that there may be relevant unpublished studies that we have not included in this review, although we believe the overall risk of publication bias is small.
Agreements and disagreements with other studies or reviews
We identified three other systematic reviews (Fehlings 2012; Kim 2015; Ozel 2016), and one recent consensus guideline (Simm 2018), on the use of bisphosphonate and other treatments for low BMD or secondary osteoporosis in children with cerebral palsy. All of these studies included lower levels of evidence from uncontrolled trials and observational studies. No study reported outcomes outside of this review; however, all the reviews also considered other treatments to improve BMD in children with cerebral palsy. All studies were consistent in their support for the use of bisphosphonate therapy in children under 18 years old with cerebral palsy and low BMD or osteoporosis.
Fehlings 2012 published a systematic review of interventions for children with cerebral palsy and low BMD. They included studies with at least 10 children under the age of 18 years with cerebral palsy and low BMD. They restricted the review to English language studies only. The review included five studies of bisphosphonates, four of intravenous pamidronate and one of oral risedronate, and all included children were non‐ambulatory (GMFCS Level IV or V). The authors included both the Henderson 2002 and Iwasaki 2008 studies in their analysis, along with two uncontrolled clinical trials and one retrospective cohort study. Four studies supported the use of bisphosphonate therapy for increasing BMD in this population. The authors concluded that overall, there was evidence of probable effectiveness (American Academy of Neurology classification level B) that bisphosphonate increases BMD in children with cerebral palsy. Two of the studies included in the review reported that bisphosphonate treatment reduced fragility fractures in children with cerebral palsy. They concluded that there was evidence of possible effectiveness (level C) to support the use of bisphosphonate to reduce the incidence of fragility fractures in children with cerebral palsy. They also noted adverse events reported by the studies, which included fever, flu‐like symptoms, and hypocalcaemia.
Ozel 2016 published an update to Fehlings 2012. They included studies of children under the age of 18 years with cerebral palsy and low BMD from January 2010 to March 2016. The updated review included one uncontrolled study and two retrospective cohort studies. Two studies supported the use of bisphosphonate to increase BMD in children with cerebral palsy; however, there was insufficient new evidence to upgrade the classification of evidence from level B (probable effectiveness). Two studies reported a reduction in fracture rate with the use of bisphosphonate therapy; however, there was insufficient new evidence to upgrade the classification from level C (possible effectiveness).
Kim 2015 completed a systematic review of bisphosphonate to treat osteoporosis in children with cerebral palsy. They included studies published in English, up to April 2014, of bisphosphonates in children under 18 years old with cerebral palsy and osteoporosis (BMD z‐score ≤ 2.0) that reported outcomes for changes in BMD z‐score. The review included four studies: Henderson 2002, and three uncontrolled trials. They found that bisphosphonate treatment improved lumbar spine BMD (standardised mean difference (SMD) 0.799, 95% CI 0.499 to 1.100), and femoral BMD (SMD 0.748, 95% CI 0.382 to 1.114).
The Simm 2018 consensus guideline on the use of bisphosphonate in children and adolescents, was published on behalf of the Australasian Pediatric Endocrine Group. It was based on the available evidence of bisphosphonates, along with other treatment options for low BMD. The authors noted that there was evidence that bisphosphonates increased BMD in people with cerebral palsy and low BMD, and highlighted the findings by Ozel 2016. They also noted the paucity of RCTs to provide conclusive evidence, and the lack of evidence regarding the effect of bisphosphonate therapy on fracture risk. They recommended yearly BMD measurement with bisphosphonate treatment lasting for longer than two years only when there was ongoing fracture risk or bone pain, and concluded that the area is in need of further research.
We also identified one additional, relevant placebo‐controlled RCT established in France, which was registered with clinicaltrials.gov; however, it was terminated after having recruited only two participants. No explanation for the termination of the trial is provided and there has been no update since 2012.
Study flow diagram
Risk of bias summary: review authors' judgements about each risk of bias item for each included study
Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies
Comparison 1: Bisphosphonate treatment versus placebo , Outcome 1: Change in BMD lumbar spine (%)
Comparison 1: Bisphosphonate treatment versus placebo , Outcome 2: Change in BMD distal femur – region 1 (%)
Comparison 1: Bisphosphonate treatment versus placebo , Outcome 3: Change in BMD distal femur – region 2 (%)
Comparison 1: Bisphosphonate treatment versus placebo , Outcome 4: Change in BMD distal femur – region 3 (%)
| Bisphosphonate treatment (oral or intravenous) compared to placebo or no treatment for children under the age of 18 with cerebral palsy (GMFCS levels III to V) | ||||||
|---|---|---|---|---|---|---|
| Patient or population: children under the age of 18 with cerebral palsy (GMFCS levels III to V) | ||||||
| Outcomes | Anticipated absolute effects* (95% CI) | Relative effect | № of participants (Studies) | Certainty of the evidence | Comments | |
| Risk with placebo or no treatment | Risk with bisphosphonate treatment (oral or intravenous) | |||||
| Change in BMD lumbar spine (%, assessed at 6 months post‐intervention) | The mean % change in BMD lumbar spine was 15% (SE ± 5%) | The mean % change in BMD lumbar spine was 18% larger in the intervention group | ‐ | 12 | ⊕⊝⊝⊝ | ‐ |
| Change in volumetric BMD of distal radius or tibia | ‐ | ‐ | ‐ | (0 studies) | ‐ | Not measured in any trial |
| Change in fracture frequency | ‐ | ‐ | ‐ | (0 studies) | ‐ | Not measured in any trial |
| Adverse events (ongoing reporting, up to 6 months post‐intervention) | 2 of 6 participants receiving their 1st 3‐day pamidronate dosing session had elevated axillary temperature (> 37 °C), but not during any subsequent dosing session. Participants receiving placebo treatment recorded no elevation in body temperature during the 1st dosing session but was noted in 4 subsequent sessions. No differences in white blood cell count were noted between treatment groups. No other adverse events were reported. | 12 | ‐ | ‐ | ||
| Change in NTX (assessed 4 to 6 months post‐intervention) | One study reported that bisphosphonate reduced serum NTX more than placebo; the other study reported that both bisphosphonate and no treatment reduced NTX (r = 0.89, P < 0.001 versus r = 0.69, P = 0.003), but did not compare groups. | 32 | ⊕⊝⊝⊝ | ‐ | ||
| Change in BAP (assessed 4 to 6 months post‐intervention) | One study reported inconclusive results between groups for BAP. The other study reported that both bisphosphonate and no treatment reduced BAP (r = 0.89, P = 0.02 versus r = 0.72, P = < 0.001), but did not compare groups. | 32 | ⊕⊝⊝⊝ | ‐ | ||
| *The risk in the intervention group (and its 95% CI) is based on the risk in the placebo or no treatment group and the relative effect of the intervention (and its 95% CI). BAP: bone‐specific alkaline phosphatase; BMD: bone mineral density; CI: confidence interval; GMFCS: Gross Motor Function Classification System; MD: mean difference; NTX: N‐telopeptides; RCT: randomised controlled trial; SE: standard error | ||||||
| GRADE Working Group grades of evidence | ||||||
| aCertainty of evidence was downgraded by two levels, one study was at high risk of bias and one study was at unclear risk of bias. | ||||||
| Section of Protocol (Zareen 2017 ) | Planned approach | Why the methods were not used |
|---|---|---|
| Types of outcome measures | We had planned to 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). | There were insufficient data from the studies identified to complete this analysis. |
| Assessment of risk of bias in included studies | We used the Cochrane RoB 1 tool when assessing the risk of bias in each domain for both included studies. Neither study was assessed as having an unclear risk of bias in all domains. In future updates of this review, we will apply the Cochrane RoB 2 tool in assessing the risk of bias for each domain in included studies, and apply the risk of bias due to missing evidence tool in assessing the risk of non‐reported evidence once the final version is released. | The review was conducted prior to the publication of updated guidelines on the assessment of risk of bias in included studies. |
| Measures of treatment effect | Dichotomous data We had intended to calculate the effect size as a risk ratio, and present it with 95% confidence intervals (CI). We had planned to consider a change as an improvement in bone mineral density (BMD) of the femur (lateral or distal), lumbar spine, and total body minus the head, measured by dual‐Energy x‐Ray absorptiometry (DXA), or volumetric BMD, measured by peripheral, quantitative computerised tomography (pQCT). | The study did not identify any relevant dichotomous data. |
| Continuous data For studies that measured the same outcome using different scales, we had planned to use the standardised mean difference (SMD) with 95% CI. | The studies used the same measures to assess the outcomes. | |
| Multiple outcomes Had studies provided multiple, interchangeable measures of the same construct at the same point in time, we would have calculated the average SMD across the outcomes and the average estimated variances (Borenstein 2009). The aim here would have been to prevent studies that reported on more outcome measures from receiving more weight in an analysis than studies that reported on only a single outcome measure. The effect estimate could have been presented as a mean difference, by transforming the SMD effect estimate backwards to one of the well‐known scales, together with a pre‐defined minimal clinically important difference. | No studies measuring multiple outcomes were identified in this review. | |
| Unit of analysis | Cluster‐randomised trials Had we identified cluster‐randomised trials, we would have sought direct estimates of the effect from an analysis that accounted for the cluster design. If the analysis had not accounted for the cluster design in the cluster trial, we would have used the approximately correct analysis approach, as presented in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2020a). | We did not identify any cluster‐randomised trials in this review. |
| Cross‐over trials We had only planned to include cross‐over trials in the meta‐analysis when the data were clear of carry‐over effects. We would have combined the results of cross‐over studies with those of parallel studies by imputing the correlation coefficient from an included study that presented individual participant data, and used this to calculate the standard deviation (SD). We would have used the generic inverse‐variance method to conduct a meta‐analysis of this data (Higgins 2020a). To avoid presenting repeated measurements reported in a study, we would have only included data from one time point from an individual study in any single meta‐analysis. | We did not identify any cross‐over trials in this review. | |
| Studies with multiple treatment groups Had we identified any studies with multiple treatment groups, we would have combined all relevant intervention groups and compared them with all relevant control groups, making single pair‐wise comparisons. If this approach had not allowed for investigation of intervention‐related sources of heterogeneity, we would have included 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 would have added the number of participants with intervention and the total number of participants, across the groups (Higgins 2020a). In case of continuous outcomes, we would have combined the mean and standard deviation using the formulae described in Chapter 10 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2020). | We did not identify any studies with multiple treatment groups. All relevant studies were a direct comparison of treatment groups to placebo or standard treatment. | |
| Dealing with missing data | If additional data had been made available, we had planned to include them in the analysis. If we received no response from the study authors, or the data were not made available, we had planned to:
We also would have specified the methods used to estimate the data in the 'Characteristics of included studies' tables and performed a Sensitivity analysis to compare the results of analyses with imputed missing data to those without imputed missing data. | It was not possible to impute missing data in the review. |
| Assessment of heterogeneity | We had planned to assess statistical heterogeneity between studies by visual inspection of the forest plot for overlapping CI, using the Chi²test 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 would have judged I² values based on the thresholds listed below, as suggested in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2020):
These thresholds can be misleading. Therefore, when considering the importance of I², we would have taken 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. Also, we would have estimated and presented Tau², along with its CI to provide an estimate of the amount of between‐study variation. | We did not assess statistical heterogeneity in this review as there were insufficient data to conduct a meta‐analysis. |
| Assessment of reporting bias | Had data from a sufficient number of studies been available (at least 10 studies in a meta‐analysis), we would have drawn funnel plots and tested for funnel plot asymmetry (Egger 1997). If we had found any asymmetry of the funnel plot, we would have looked for possible causes (such as publication bias or true heterogeneity) that we might have considered to have a likely influence on the observed effect sizes in our interpretation of the results. However, given that common tests of publication bias lack sensitivity, we would have considered the possible influence that a dominance of small trials might have had on pooled effect sizes in our interpretation, where indicated. | We could not assess reporting bias by drawing funnel plots and testing for funnel plot asymmetry due to an insufficient number of included studies. |
| Data synthesis | If sufficient data had been included, we would have conducted a meta‐analysis. As we would have expected some heterogeneity in intervention characteristics, we would have pooled the available data using the random‐effects model (Deeks 2020). 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 would have conducted a sensitivity analysis using the fixed‐effect model. | We could not complete a meta‐analysis due to insufficient data and so provided a narrative description of the results instead. |
| Subgroup analysis and investigation of heterogeneity | We had planned to perform the following subgroup analyses:
| There were insufficient data to conduct subgroup analyses. |
| Sensitivity analysis | We had planned to perform a sensitivity analysis if there were sufficient data (10 or more studies). Our plan was to:
| We did not perform a sensitivity analysis due to an insufficient number of included studies. |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1.1 Change in BMD lumbar spine (%) Show forest plot | 1 | Mean Difference (IV, Fixed, 95% CI) | Totals not selected | |
| 1.2 Change in BMD distal femur – region 1 (%) Show forest plot | 1 | Mean Difference (IV, Fixed, 95% CI) | Totals not selected | |
| 1.3 Change in BMD distal femur – region 2 (%) Show forest plot | 1 | Mean Difference (IV, Fixed, 95% CI) | Totals not selected | |
| 1.4 Change in BMD distal femur – region 3 (%) Show forest plot | 1 | Mean Difference (IV, Fixed, 95% CI) | Totals not selected | |
