Monitorización con espectroscopia del infrarrojo cercano cerebral para la prevención de lesiones cerebrales en lactantes muy prematuros
Resumen
Antecedentes
La lesión cerebral y la deficiencia del desarrollo nervioso a largo plazo son frecuentes en los lactantes muy prematuros. La espectroscopia del infrarrojo cercano cerebral (EICC) permite la estimación continua de la oxigenación cerebral. Este método diagnóstico en conjunto con las intervenciones apropiadas, si la EICC está fuera del rango normal (que es una oxigenación cerebral dentro del 55% al 85%), puede proporcionar efectos beneficiosos sin causar más efectos perjudiciales. Por lo tanto, es necesario evaluar la EICC en conjunto con respuestas apropiadas a hallazgos anormales de la EICC en una revisión sistemática de ensayos clínicos aleatorizados y estudios cuasialeatorizados.
Objetivos
Evaluar los efectos beneficiosos y perjudiciales de las intervenciones que intentan modificar la oxigenación cerebral guiadas por monitorización cerebral con EICC para prevenir la lesión cerebral, mejorar el desenlace neurológico y aumentar la supervivencia en los lactantes prematuros nacidos más de ocho semanas antes del término.
Métodos de búsqueda
Se utilizó la estrategia de búsqueda estándar del Grupo Cochrane de Neonatología (Cochrane Neonatal Review Group) para buscar en el Registro Cochrane Central de Ensayos Controlados (Cochrane Central Register of Controlled Trials) (CENTRAL 2016, número 8), MEDLINE vía PubMed (1966 hasta 10 septiembre 2016), Embase (1980 hasta 10 septiembre 2016) y en CINAHL (1982 hasta 10 septiembre 2016). También se buscaron ensayos clínicos aleatorizados y estudios cuasialeatorizados en las bases de datos de ensayos clínicos, actas de congresos y en las listas de referencias de los artículos recuperados.
Criterios de selección
Ensayos clínicos aleatorizados y estudios clínicos cuasialeatorizados que compararon la monitorización cerebral continua con EICC durante al menos 24 horas frente a la EICC cegada o ninguna monitorización con EICC.
Obtención y análisis de los datos
Dos autores de la revisión, de forma independiente, seleccionaron, evaluaron la calidad y extrajeron los datos de los ensayos y estudios incluidos. En caso necesario, se contactó con los autores para obtener información adicional. Se realizaron evaluaciones de los riesgos de sesgo; de los riesgos de errores de diseño; y se controlaron los riesgos de errores aleatorios con el Análisis Secuencial de Ensayos (TSA, por sus siglas en inglés). Se evaluó la calidad de la evidencia mediante GRADE.
Resultados principales
Un ensayo clínico aleatorizado cumplió con los criterios de inclusión y reclutó lactantes nacidos más de 12 semanas antes del término. El ensayo empleó metodologías adecuadas y se consideró con bajo riesgo de sesgo. Ciento sesenta y seis lactantes se asignaron al azar a comenzar la monitorización cerebral continua con EICC antes de las tres horas después del nacimiento hasta 72 horas después del nacimiento, más intervenciones apropiadas si la EICC estuviera fuera del rango normal según una guía frente a la monitorización convencional con EICC cegada. No hubo efecto de la EICC más la guía sobre la mortalidad hasta la edad equivalente al término (RR: 0,50; IC del 95%: 0,29 a 1,00; un ensayo; 166 participantes). No hubo efectos de la EICC más la guía sobre las hemorragias intraventriculares: todos los grados (RR 0,93; IC del 95%: 0,65 a 1,34; un ensayo; 166 participantes); grado III/IV (RR 0,57; IC del 95%: 0,25 a 1,31; un ensayo; 166 participantes); y leucomalacia periventricular quística (que no presentó ninguno de los grupos). Asimismo, no hubo ningún efecto de la EICC más la guía sobre la aparición de un conducto arterioso persistente (RR: 1,96; IC del 95%: 0,94 a 4,08; un ensayo; 166 participantes); enfermedad pulmonar crónica (RR: 1,27; IC del 95%: 0,94 a 1,50; un ensayo; 166 participantes); enterocolitis necrotizante (RR: 0,83; IC del 95%: 0,33 a 1,94; un ensayo; 166 participantes); y retinopatía del prematuro (RR: 1,64; IC del 95%: 0,75 a 3,00; un ensayo; 166 participantes). No hubo eventos adversos graves en ninguno de los grupos de intervención. La EICC más la guía provocaron más marcas en la piel por el sensor de EICC en el grupo control que en el grupo experimental (RR no ajustado: 0,31; IC del 95%: 0,10 a 0,92; un ensayo; 166 participantes). No hay datos con respecto al desenlace de desarrollo nervioso, la insuficiencia renal ni las fugas de aire.
La calidad de la evidencia de todas las comparaciones analizadas anteriormente se consideró muy baja, excepto en el caso de la mortalidad por todas las causas y los eventos adversos: baja y moderada, respectivamente. La validez de todas las comparaciones estuvo limitada por la muestra pequeña de lactantes asignados al azar, el riesgo de sesgo debido a la falta de cegamiento y las medidas indirectas de los desenlaces.
Conclusiones de los autores
El único ensayo clínico aleatorizado elegible no demostró efectos consistentes de la EICC más una guía sobre los desenlaces clínicos evaluados. Sin embargo, el ensayo solamente tuvo potencia estadística para detectar diferencias en la oxigenación cerebral, no en la morbilidad ni la mortalidad. Esta revisión sistemática no alcanzó una potencia estadística suficiente para probar ni refutar efectos sobre los desenlaces clínicos. Se necesitan ensayos clínicos aleatorizados adicionales con bajo riesgo de sesgo y bajo riesgo de errores aleatorios.
PICOs
Resumen en términos sencillos
Monitorización con espectroscopia del infrarrojo cercano cerebral para la prevención de lesiones cerebrales en lactantes muy prematuros
Pregunta de la revisión
Para determinar los efectos beneficiosos y perjudiciales de la estimación continua no invasiva de los niveles de oxígeno del tejido cerebral mediante la espectroscopia del infrarrojo cercano (EICC) sobre la mortalidad y el desarrollo posterior en los lactantes nacidos con más de ocho semanas pretérmino.
Antecedentes
Los lactantes nacidos con más de ocho semanas antes del término tienen riesgo de sufrir lesión cerebral y deficiencia del desarrollo. La EICC permite medir de forma continua el contenido de oxígeno del tejido cerebral emitiendo diferentes ondas de luz en el rango del infrarrojo cercano en el tejido y midiendo la intensidad de la luz reflejada a unos pocos centímetros de la fuente de luz. Se ha propuesto que evitar niveles de oxígeno muy bajos o muy altos en el cerebro podría tener efectos beneficioso para estos pequeños lactantes.
Características de los estudios
En la evidencia actual hasta septiembre de 2016, se encontró un ensayo que evaluó principalmente si la oxigenación cerebral se puede estabilizar al combinar las mediciones en el cerebro mediante la EICC con una guía de tratamiento sobre cómo intervenir cuando la oxigenación cerebral está fuera el rango normal. Los 166 lactantes incluidos nacieron con más de 12 semanas antes del término. Se monitorizaron durante los tres primeros días de vida. El estudio fue financiado por una agencia gubernamental y se encontró que los métodos utilizados en el ensayo fueron los mejores posibles.
Resultados clave
El único ensayo encontrado mostró una diferencia grande y significativa en la oxigenación cerebral entre el grupo experimental y el grupo control. La oxigenación baja fue mucho más frecuente en el grupo control. Sin embargo, dicho ensayo no encontró que la monitorización con EICC reduzca la mortalidad ni la aparición de las complicaciones más frecuentes del nacimiento muy prematuro, es decir, hemorragias intracraneales, enfermedad pulmonar crónica, daño a los intestinos (enterocolitis necrosante) y ceguera (retinopatía del prematuro).
La monitorización con EICC no provocó daños graves, pero se observaron marcas en la piel debido al sensor de la EICC en cerca de uno de cada diez pacientes.
Calidad de la evidencia
La información obtenida con un ensayo aleatorizado de pequeño tamaño es demasiado poca para sacar conclusiones acerca de los efectos beneficiosos y perjudiciales de la espectroscopia del infrarrojo cercano cerebral en los lactantes prematuros. Por lo tanto, se necesitan estudios adicionales.
Authors' conclusions
Summary of findings
| Cerebral NIRS oximetry compared to no cerebral NIRS oximetry in very preterm infants | ||||||
| Patient or population: prevention of morbidities in very preterm infants | ||||||
| Outcomes | Anticipated absolute effects* (95% CI) | Relative effect | № of participants | Quality of the evidence | Comments | |
| Risk with control | Risk with Cerebral NIRS oximetry | |||||
| All‐cause mortality | Study population | RR 0.50 | 166 | ⊕⊕⊝⊝ | ||
| 250 per 1000 | 125 per 1000 | |||||
| Intraventricular haemorrhage grade III or IV | Study population | RR 0.57 | 166 | ⊕⊝⊝⊝ | ||
| 163 per 1000 | 93 per 1000 | |||||
| Cystic periventricular leukomalacia (diagnosed by cranial ultrasound) | Study population | not estimable | 166 | ⊕⊝⊝⊝ | ||
| 0 per 1000 | 0 per 1000 | |||||
| Patent ductus arteriosus | Study population | RR 1.96 | 166 | ⊕⊝⊝⊝ | ||
| 113 per 1000 | 221 per 1000 | |||||
| Chronic lung disease (oxygen supplementation at 36 weeks' postmenstrual age) | Study population | RR 1.27 | 132 | ⊕⊝⊝⊝ | ||
| 467 per 1000 | 593 per 1000 | |||||
| Proven necrotising enterocolitis (Bell's stage II or III) | Study population | RR 0.83 | 166 | ⊕⊝⊝⊝ | ||
| 125 per 1000 | 104 per 1000 | |||||
| Retinopathy of prematurity, any or severe (stage ≥ III) | Study population | RR 1.64 | 166 | ⊕⊝⊝⊝ | ||
| 100 per 1000 | 164 per 1000 | |||||
| Other adverse effects | Study population | not estimable | 166 | ⊕⊝⊝⊝ | ||
| 0 per 1000 | 0 per 1000 | |||||
| *The risk in the intervention group (and its 95% CI) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1 Optimal information size not met. 2 Treatment group allocation not blinded. 3 Surrogate outcome close in the causal pathway to patient‐important outcomes. 4 Surrogate outcome far removed in the causal pathway from patient‐important outcomes. | ||||||
Background
Description of the condition
Preterm birth carries a high risk of cerebral impairment and death. Twenty‐five per cent of infants born more than 12 weeks before term die before being discharged from the hospital, and about 25% of survivors will suffer from cerebral palsy or other neurodevelopmental delays (Volpe 2009).
The aetiology behind the long‐term complications of preterm birth is multifactorial. It is believed that cerebral hypoxia‐ischaemia is important (Whitelaw 2001). Hypoxia‐ischaemia represents a mismatch between cerebral oxygen supply and demand that may be caused by, for example, hypotension (Munro 2004), low systemic blood flow (Takami 2010), increased cerebral oxygen demand, or low arterial blood oxygen content. Conversely, it has been suggested that too much oxygen to the immature brain is deleterious (Deulofeut 2006).
Specific brain lesions thought to be associated with hypoxia‐ischaemia include germinal matrix haemorrhage, interventricular haemorrhage (Verhagen 2010), and periventricular leukomalacia (Khwaja 2008; Kuint 2009).
To prevent or minimise permanent neurological damage from hypoxia‐ischaemia or hyper‐oxygenation, immediate and appropriate interventions are essential. This remains a challenge as cerebral hypoxia‐ischaemia often passes silently without many clinical signs or symptoms (Highton 2010).
Description of the intervention
Near‐infrared spectroscopy (NIRS) enables a measurement of an absolute value of regional tissue haemoglobin oxygen saturation (rStO₂) (Wolf 2009). rStO₂ represents a weighted average of arterial and venous oxygen saturation. The weight is commonly assumed to be 25% arterial and 75% venous, but may vary within and among patients (Watzman 2000). A reference standard remains to be established. Several studies have found a significant correlation between rStO₂ measured by cerebral NIRS and venous jugular bulb blood oxygen saturation, but the agreement is generally poor with about plus or minus 17 percentage points limits of agreement (Buunk 1998; Nagdyman 2005), possibly reflecting the fact that NIRS is a volume‐weighted measurement, whereas jugular bulb oxygen saturation is a flow‐weighted one.
The relationship between cerebral rStO₂ and brain damage has been assessed in several piglet studies. It seems that both the magnitude of cerebral rStO₂ deviation from baseline and the duration of deviation matter (Hou 2007; Kurth 2002; Kurth 2009). It is thus reasonable to assume that the rStO₂ must be kept within a safe range and that brief or minor deviations from that range are harmless.
Data on the clinical significance of cerebral rStO₂ are still rather scant. In adults, Heringlake and colleagues found that a pre‐cardiac surgery cerebral rStO₂ less than 50% was an independent risk factor for 30‐day and 1‐year mortality (Heringlake 2010). Furthermore, intraoperative desaturation during cardiac surgery has been shown to be associated with post‐operative cognitive dysfunction (de Tournay‐Jetté 2011; Slater 2009).
In infants, Toet and colleagues found that rStO₂ was a predictor of neurodevelopmental outcome in term newborns suffering from hypoxic‐ischaemic encephalopathy (Toet 2006). Children with adverse outcomes had a significantly elevated cerebral rStO₂ at 24 hours postpartum compared to infants with normal outcome. In preterm infants, Sorensen and colleagues saw a correlation between the degree of cerebral hypoxia estimated by NIRS and the severity of brain damage (Sorensen 2006). The association between low rStO₂ and cerebral injury was also found by two other studies in preterm infants (Balegar 2014; Verhagen 2010). In accordance with these findings, Alderlisten and colleagues found that having a rStO₂ below 50% for more than 10% of the time during the first 3 days of life was associated with a 5 point lower developmental quotient (Alderliesten 2014).
The precise safe range of cerebral rStO₂ is not established, and both inter‐ and intravariance is likely. In adults undergoing surgery, thresholds for intervention are dependent on the pre‐surgery baseline rStO₂, for example to intervene when rStO₂ has dropped 20 percentage points (Denault 2007). For preterm infants, who can be haemodynamically unstable from birth, the usefulness of such a baseline measurement is less evident. Thresholds for intervention must rely on the absolute values of rStO₂, like pulse oximetry‐guided adjustment of the fraction of inspired oxygen (Finer 2010). It is then a problem that the repeated measures within subject standard deviation is about 5% to 6% (Hyttel‐Sorensen 2011; Sorensen 2006), while there is a systematic bias between sensors from INVOS 5100 and NIRO 300 (Dullenkopf 2003). In addition, Hessel and colleagues found that INVOS 5100 and FORE‐SIGHT show increasing difference in rStO₂ estimate with decreasing oxygenation in infants (Hessel 2014).
There is now accumulating evidence that it is possible to minimise cerebral desaturation in adults undergoing cardiac surgery (Deschamps 2016; Murkin 2007), and non‐cardiac surgery (Casati 2005). It remains to be established if this improves patient‐relevant outcomes.
The focus of the current review is the cerebral NIRS in neonatal intensive care units. The optimal timing of monitoring in preterm infants has not been determined, but it should follow the notion that cerebral NIRS monitoring has to be continuous if it is to have the greatest possible impact on clinical outcomes. Moreover, as the first week of life is the most vulnerable in respect to low cerebral blood flow and brain damage (Meek 1999; Perlman 2000; Volpe 2009), early NIRS monitoring within hours or a few days of birth is likely to be most efficient (Greisen 2011). Most NIRS devices estimate the rStO₂ every 5 seconds, but the clinical interpretation is based not only on the current absolute cerebral rStO₂ value, but perhaps even more so on the trend in rStO₂ over minutes and hours.
NIRS‐guided intensive care is a complex intervention as it consists of monitoring a physiological quantity (similar to a diagnostic test) coupled with a number of possible specific interventions either given alone or in concert. In other words, NIRS monitoring will have no impact on clinical outcomes if it does not lead to changes in clinical management. In a trial setting, a pre‐specified treatment guideline will most likely increase the likelihood that out‐of‐range cerebral rStO₂ values are dealt with in a consistent manner. The appropriateness of the treatment guideline also depends on whether it defines cerebral rStO₂ thresholds for intervention, if these thresholds are appropriate, and if there is a clear guidance on how to react when outside these thresholds. For comparison, with pulse oximetry, a target range of 85% to 89% saturation has been shown to be associated with a lower survival rate compared to a target range of 91% to 95% in the extremely preterm population (Stenson 2011). Cerebral rStO₂ is a more complex physiological quantity than oxygen saturation (SpO₂), and its safe ranges are likely to be broader. Furthermore, as described above, the appropriate rStO₂ thresholds could well be device‐dependent. The quality of the overall intervention depends on the NIRS monitoring and the treatment guideline describing how to normalise the rStO₂ as well as adherence to the guideline; differences in compliance could be a sources of heterogeneity. Although quality of interventions should be incorporated in a meta‐analysis of complex interventions (Herbert 2005), there is no generally accepted framework for such an analysis. Moreover, few trial reports provide sufficient detail on how to assess the quality of the intervention (Boutron 2008). We suggest subgroup analyses based on duration of NIRS monitoring, assessment of trial treatment guideline, and adherence to these guidelines to assess the quality of the intervention.
Adverse effects directly relating to the NIRS device are similar to those of the widely applied pulse oximetry, that is primarily local skin damages such as burns, pressure sores, and skin irritation (Hyttel‐Sorensen 2013a). Another concern is that NIRS‐driven interventions could be deleterious. The SpO₂ level is related to the rStO₂, and it is likely not appropriate to aim for SpO₂ higher than the normal target range in order to increase a low rStO₂. It could lead to a higher incidence of retinopathy.
How the intervention might work
Cerebral NIRS monitoring could benefit the clinical outcomes of preterm infants because NIRS has the potential to alert healthcare workers when cerebral hypoxia or hyperoxia occurs. Cerebral rStO₂ is dependent on three variables: oxygen delivery to the brain, cerebral oxygen consumption, and the arterial‒venous volume ratio. The second variable is not easily controlled in preterm infants and the third variable is not relevant for oxygen sufficiency of the brain, so interventions guided by cerebral oxygenation in preterm infants focus on oxygen delivery to the brain, that is the oxygen content of arterial blood, cerebral blood flow, or the combination of both. Interventions that alter the oxygen content include changing the fractional inspiratory oxygen or elevating the haematocrit by blood transfusion, while cerebral blood flow can be affected by changing mean airway pressure and ventilatory rate during mechanical ventilation or by increasing blood pressure and cardiac output by fluid or vasopressors or inotropes. Observation of abnormal values could thus motivate reactive interventions such as changes in ventilator settings and initiation of haemodynamic support. The possible relevant interventions depend on the situation at hand (Pellicer 2013). The main goal is to respond to the NIRS measurement of cerebral rStO₂ in order to initiate treatments that are known to normalise cerebral blood flow or blood oxygen content (Denault 2007).
Why it is important to do this review
Despite the lack of firm evidence and the potential limitations of NIRS, the monitoring technique is increasingly implemented in clinical routine care of preterm infants. A review on the use of NIRS in congenital heart disease found four randomised clinical trials, but none of them reported on important patient‐relevant clinical outcomes (Hirsch 2009). A systematic review of the evidence of benefits and harms in preterm infants is needed to establish the available support behind this new tool.
This review is based on our published protocol (Hyttel‐Sorensen 2015b).
Objectives
To evaluate the benefits and harms of interventions that attempt to alter cerebral oxygenation guided by cerebral NIRS monitoring in order to prevent cerebral injury, improve neurological outcome, and increase survival in preterm infants born more than 8 weeks preterm.
In subgroup analyses, we plan to examine the effectiveness and safety of NIRS‐guided treatments in relation to the following criteria: gestational age (GA), quality of intervention, i.e. duration of NIRS monitoring, assessment of trial treatment guideline, and adherence to these guidelines, and level of support during the first seven days of life.
Methods
Criteria for considering studies for this review
Types of studies
We included all randomised clinical trials and quasi‐randomised clinical studies irrespective of language and publication status.
Types of participants
Infants born before 32 weeks of gestational age (GA). We included both singletons and infants from multiple births (see Unit of analysis issues section). We chose the cut‐off at 32 weeks because the risk associated with preterm birth including brain injury increases with decreasing GA (MacKay 2010; Mohangoo 2011).
Types of interventions
Continuous cerebral NIRS monitoring versus blinded NIRS monitoring or versus conventional monitoring with no NIRS during intensive care. The monitoring should start within one week from birth, be continuous, and last for at least 24 hours.
We included trials where detection of rStO₂ values lead to changes in treatment in the experimental group.
The only prerequisite for the NIRS equipment was that it had to show a value for tissue oxygenation in percentage similar to arterial haemoglobin oxygen saturation. If several different brands of NIRS devices were used in a specific trial, this had to be addressed in the randomisation process to ensure equal distribution of the device intervention among groups.
The control group could use conventional monitoring such as invasive or non‐invasive blood pressure monitoring, pulse oximetry, electrocardiographic monitoring, and/or transcutaneous oxygen partial pressure (pO₂) and carbon dioxide partial pressure (pCO₂) monitoring without the use of NIRS or with NIRS monitoring where the rStO₂ values were concealed to the treating healthcare workers.
Concomitant interventions or treatments were allowed provided that the intervention groups were offered these treatments equally.
We planned to exclude studies where NIRS monitoring is part of multi‐monitoring, that is trials where other monitoring modalities than NIRS differ between groups.
Types of outcome measures
Primary outcomes
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All‐cause mortality: neonatal mortality (death during the first 28 days of life) and during the first year of life.
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Major neurodevelopmental disability.
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Cerebral palsy.
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Severe neurodevelopmental impairment as evaluated by validated developmental assessment tool, e.g. more than 2 standard deviations (SD) below the mean in Bayley Scales of Infant Development.
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Blindness (vision < 6/60 in both eyes).
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We planned to report these components of long‐term outcome for all studies that have evaluated children after 18 months' chronological age, and to perform separate analyses for children aged 18 to 24 months and 3 to 5 years.
Secondary outcomes
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Use of interventions with possible impact on cerebral oxygenation. Interventions to normalise rStO₂ that may act as effect modifiers on the outcomes at 7 and 28 days of life.
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Number of changes in mean airway pressure per time‐unit (i.e. to increase or decrease continuous positive airway pressure or positive end‐expiratory pressure).
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Number of changes per time‐unit in inspiratory oxygen fraction FiO₂.
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Number of changes per time‐unit in blood pCO₂ (i.e. to change ventilation by changing respiratory rate on mechanically ventilated infants).
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Number of changes per time‐unit in vasopressor or inotrope dosage, or both (i.e. to initiate, stop, increase, or decrease the use of vasopressors/inotropic agents).
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Number of fluid bolus treatments (i.e. to give a bolus of fluid at 5 to 20 ml/kg body weight) to increase systemic blood circulation per time‐unit.
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Number of blood transfusions administered.
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Number of patent ductus arteriosus treatments (i.e. attempt to close the duct medically or surgically) received.
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Morbidities.
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Intraventricular haemorrhage (all grades) (Papile 1978).
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Intraventricular haemorrhage grade III or IV (Papile 1978).
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Cystic periventricular leukomalacia (diagnosed by cranial ultrasound).
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Patent ductus arteriosus diagnosed by echocardiography.
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Renal impairment (creatinine ≥ 120 μmol/L, oliguria ≤ 0.5 ml/kg/hour at 1 week of age).
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Air leak (any and gross including pneumothorax or pneumomediastinum).
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Chronic lung disease (oxygen supplementation at 36 weeks' postmenstrual age).
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Proven necrotising enterocolitis (Bell's stage II or III) (Bell 1978).
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Retinopathy of prematurity, any or severe (stage ≥ III) (International Committee 2005).
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Adverse events.
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Skin marks at term considered to be caused by the NIRS monitoring.
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Adverse effects not listed as an outcome above but reported by the authors as an adverse event.
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Search methods for identification of studies
Electronic searches
We used the criteria and standard methods of Cochrane and the Cochrane Neonatal Review Group (see the Cochrane Neonatal Group search strategy for specialized register).
We conducted a comprehensive search including: Cochrane Central Register of Controlled Trials (CENTRAL; 2016, Issue 8) in The Cochrane Library; MEDLINE via PubMed (1996 to 10 September 2016); Embase (1980 to 10 September 2016); and CINAHL (1982 to 10 September 2016) using the following search terms: (NIRS OR near‐infrared spectroscope OR near infrared spectroscopy), plus database‐specific limiters for randomised controlled trials (RCTs) and neonates (see Appendix 1 for the full search strategies for each database). We did not apply any language restrictions.
We searched clinical trial registries for ongoing or recently completed trials (ClinicalTrials.gov; the World Health Organization’s International Clinical Trials Registry Platform www.who.int/ictrp/search/en, and the ISRCTN Registry).
Searching other resources
We asked experts in the NIRS field about their knowledge of unpublished randomised clinical trials.
Data collection and analysis
Selection of studies
Two review authors (SHS and GG) independently assessed the trials for eligibility. Excluded trials and reasons for exclusion are in the 'Characteristics of excluded studies' table. SHS and GG would have involved a third review author in the event of disagreements.
Data extraction and management
Two review authors (SHS and GG, independently validated by BAN) independently extracted information on each trial including data concerning trial design, participants, interventions, and outcomes as detailed in the selection criteria described above.
Assessment of risk of bias in included studies
We assessed bias according to each domain of bias described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We regarded trials at low risk of bias if all of the following criteria were fulfilled: adequate generation of allocation sequence, adequate allocation concealment, adequate blinding, adequate outcome measure reporting, and analysis performed by intention to treat, no vested interest, no recruitment bias, and no other sources of bias. We considered blinding adequate if the outcome assessors were blinded to the type of intervention (allocation group).
Two review authors (SHS and GG) independently assessed the risk of bias in each trial.
We assessed risk of bias according to the following domains (Higgins 2011; Lundh 2017; Savović 2012a; Savović 2012b; Wood 2008).
Sequence generation
Low risk: the investigators described a random component in the sequence generation process such as coin toss, card draw, etc.
High risk: the investigators describe a nonrandom component in the sequence generation process. This would typically involve a systematic, nonrandom approach like sequence generated by date of birth. We planned to exclude such studies for assessment of benefits and safety.
Unclear: insufficient information about the sequence generation process to permit judgement of ‘low’ or ‘high’ risk.
Allocation concealment
Low risk: participants and investigators enrolling participants could not foresee assignment due to central allocation (telephone or web‐based).
High risk: participants or investigators enrolling participants could possibly foresee assignments. We planned to exclude such studies for assessment of benefits.
Unclear: insufficient information to permit judgement of ‘low’ or ‘high’ risk.
Blinding of participants, personnel, and outcome assessors
Preterm infants are de‐facto blinded, but due to the nature of the intervention blinding of the participants and personnel is impossible.
Low risk: participants, personnel and outcome assessors were blinded. Method of blinding is described.
High risk: no or incomplete blinding of one or more of 'participants', 'personnel', and 'outcome assessors'.
Unclear: insufficient information to permit judgement of ‘low’ or ‘high’ risk.
Incomplete outcome data
Low risk: no missing outcome data, or reasons for missing outcome data unlikely to be related to true outcome. Missing outcome data balanced across intervention groups.
High risk: number of or reasons for dropouts and withdrawals were not described.
Unclear: insufficient reporting of attrition/exclusions to permit judgement of ‘low’ or ‘high’ risk.
Selective outcome reporting
Low risk: the study protocol is available and all of the study’s pre‐specified (primary and secondary) outcomes that are of interest in the review have been reported in the pre‐specified way.
High risk: not all of the trial's pre‐specified outcomes have been reported. One or more primary outcomes are reported using measurements, analysis methods, or subsets of the data (e.g. subscales) that were not pre‐specified. One or more reported primary outcomes were not pre‐specified.
Unclear: insufficient information to permit judgement of ‘low’ or ‘high’ risk.
Vested interest bias
Low risk: the trial’s funding was not from parties that might have conflicting interest.
High risk: trial funded by a medical device manufacturer.
Unclear: source of funding not described.
Recruitment bias
Assessment was only applicable for studies including twins.
Low risk: individuals in a cluster were randomised and allocated together.
High risk: second twin was included after the first has been randomised.
Unclear: insufficient information to permit judgement of ‘low’ or ‘high’ risk.
Other sources of bias
Low risk: the study appears to be free of other sources of bias.
High risk: there was at least one important risk of bias. For example, the study had a potential source of bias related to the specific study design used, or has been claimed to have been fraudulent, or had some other problem.
Unclear: there may be a risk of bias, but insufficient information to permit judgement of ‘low’ or ‘high’ risk.
Overall risks of bias
We considered trials to be at low risk of bias if all of the above domains were deemed low risk. Per‐protocol, all other studies were to be regarded at high risk of bias.
We restricted the meta‐analysis to trials at low risk of bias (Higgins 2011); however, we also included trials that had high risk of performance bias, but where outcome assessors were blinded adequately.
Measures of treatment effect
We present dichotomous outcomes as risk ratio (RR) with naive 95% confidence intervals (CI) and planned to calculate Trial Sequential Analysis‐adjusted CI (Thorlund 2011; Wetterslev 2017). Values less than 1.00 favour NIRS‐guided treatment. We planned to report continuous neurological outcomes data as weighted mean difference with naive 95% CI and Trial Sequential Analysis‐adjusted CI in case different scales were used. We planned to calculate the risk difference (RD) and 95% CI and convert the RD into the number needed to treat for an additional beneficial outcome or the number needed to treat for an additional harmful outcome if statistically significant intervention effects were found. We planned to analyse continuous data using mean difference (MD).
Unit of analysis issues
Trials including twins in the same intervention group are cluster trials unless data from only one of the twins are used in the analysis in a randomised fashion. Data from twins cannot be assumed to be independent from one another. Appropriate statistical analysis will take this into account. In a meta‐analysis, trials where the analysis does not account for the twin correlation will receive more weight than appropriate. In cluster‐randomised trials, the following biases must be considered: i) recruitment bias; ii) baseline imbalance; iii) loss of clusters; iv) incorrect analysis; and v) comparability with individually randomised trials.
We describe assessment of risk of recruitment bias above. The risk of baseline imbalance and loss of clusters is negligible as studies including twins are characterised by many small clusters. We assessed included trials for appropriate analyses. If clusters were not accounted for, inflation of the standard errors would be done according to Section 16.3.6 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).
Dealing with missing data
We planned to contact the original investigators and authors for any missing data then use a 'complete‐participant analysis' by excluding all participants with the outcome missing from the analysis, and lastly perform a sensitivity analysis (see Sensitivity analysis section).
Assessment of heterogeneity
We planned to test for statistical heterogeneity using the Chi² test with significance set at P < 0.1; and quantify inconsistency by I², which describes the percentage of the variability in effect estimates that is due to heterogeneity rather than sampling error (chance). The degree of heterogeneity was defined as: no heterogeneity ‒ less than 25%; low heterogeneity ‒ 25% to 49%; moderate heterogeneity ‒ 50% to 74%; high heterogeneity ‒ 75% and above. We intended to explore the possible causes of statistical heterogeneity, using planned and post hoc subgroup analyses.
Assessment of reporting biases
We planned to assess reporting biases using funnel plots of the effect estimates using Review Manager 5 (RevMan 2014) software if 10 or more studies were included.
Data synthesis
We planned to do a fixed‐effect model meta‐analysis in accordance with the Cochrane Handbook for Systematic Reviews of Interventions, and summarise data statistically if available, sufficiently similar, and of sufficient quality.
If the estimated heterogeneity using the Chi² test was I² greater than 25%, we would carry out a random‐effects model meta‐analysis to compare to the fixed‐effects estimates of the intervention effect. This is in accordance with Section 10.4.4.1 of the Cochrane Handbook for Systematic Reviews of Interventions.
In assessing the treatment effects for dichotomous outcomes, we planned to use the RR and RD, with naive 95% CI and RR Trial Sequential Analysis‐adjusted CI; and for outcomes measured on a continuous scale, we planned to use the MD, with naive 95% CI and Trial sequential Analysis‐adjusted CI.
For binary and continuous outcome measures, we intended to conduct Trial Sequential Analysis (TSA) in order to calculate the desired quantity of information and the cumulative Z‐curve’s breach of relevant trial sequential monitoring boundaries (Wetterslev 2008). For binary outcomes, we planned to estimate the required information size based on the proportion of participants with an outcome in the control group, a RR suggested by the trials with low risk of bias; or if not possible a relative risk reduction (RRR) of 20%, an alpha of 5%, a beta of 10%, and diversity of 30% and 60%. For continuous outcomes, we estimated the required information size based on the SD observed in the control group of trials with low risk of bias and a minimal relevant difference of 25% of this SD, an alpha of 5%, a beta of 10%, and diversity of 30% and 60%.
Subgroup analysis and investigation of heterogeneity
In subgroup analyses we planned to examine the effectiveness and safety of NIRS‐guided treatment in relation to the following criteria: gestational age, duration of NIRS monitoring, and quality of intervention.
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Gestational age (GA): possibly extracted from subgroups within each trial; GA ≤ 28 weeks compared to GA > 28 weeks.
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Duration of NIRS monitoring: the trials were to be ranked from shortest to longest NIRS duration and the subgroups defined as below the median or equal to and above the median.
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Quality of intervention: high‐quality intervention trials compared to low‐quality intervention trials.
For the third bullet point above, high‐quality intervention trials would have been defined as follows: the treatment guideline gives device‐specific, pre‐specified ranges of rStO₂ with guidance on when to intervene and a pre‐specified treatment algorithm incorporating guidance on respiratory and cardiovascular care including target ranges of SpO₂, blood pressure, and pCO₂; the final publication reports on the duration of NIRS monitoring, methods to standardise the intervention across centres or practitioners, adherence‐improving strategies, and description of treatment in the comparator group.
For the third bullet point above, low‐quality intervention trials would have been defined as follows: unclear or no defined ranges of rStO₂ or no specified treatment algorithm, or the algorithm does not incorporate guidance on respiratory and cardiovascular care; proper procedures to standardise the intervention or to insure adherence to protocol are lacking or not described; no report on duration of NIRS monitoring; no description of treatment in comparator group.
We planned to conduct a test of interaction of fixed‐effect model meta‐analyses of the subgroups according to Altman and Bland (Altman 2003).
Sensitivity analysis
We planned to perform a sensitivity analysis to determine the influence of the bias quality criteria.
For missing data, we planned to conduct sensitivity analyses for our primary outcomes by applying best‐ and worst‐case scenarios. The best‐case scenario: all participants lost to follow‐up in the experimental group had a beneficial outcome, and all participants lost to follow‐up in the control group had the opposite. The worst‐case scenario: all participants lost to follow‐up in the experimental group had a detrimental outcome, and all participants lost to follow‐up in the control group had a beneficial outcome.
Quality of evidence
We used the GRADE approach, as outlined in the GRADE Handbook (Schünemann 2013), to assess the quality of evidence for the following (clinically relevant) outcomes: all‐cause mortality; major neurodevelopmental disability; intraventricular haemorrhage (all grades); intraventricular haemorrhage grade III or IV; cystic periventricular leukomalacia; patent ductus arteriosus; renal impairment; air leak; chronic lung disease; necrotising enterocolitis; retinopathy of prematurity, any or severe (stage ≥ III); skin marks at term considered to be caused by the NIRS monitoring; adverse effects not listed as an outcome above but reported by the authors as an adverse event (see Types of outcome measures for diagnostic criteria).
Two authors independently assessed the quality of the evidence for each of the outcomes above. We considered evidence from randomised clinical trials as high quality but downgraded the evidence one level for serious (or two levels for very serious) limitations based upon the following: design (risk of bias), consistency across studies, directness of the evidence, precision of estimates, and presence of publication bias. We used the GRADEpro GDT Guideline Development Tool to create a ‘Summary of findings’ table to report the quality of the evidence.
The GRADE approach results in an assessment of the quality of a body of evidence in one of four grades:
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High: we are very confident that the true effect lies close to that of the estimate of the effect.
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Moderate: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.
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Low: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect.
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Very low: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate of effect.
Results
Description of studies
See: Characteristics of included studies; Characteristics of excluded studies.
Results of the search
Only one randomised clinical trial was identified that compared continuous cerebral NIRS monitoring plus a guideline versus conventional NICU monitoring plus blinded NIRS in preterm infants (Hyttel‐Sorensen 2015a) Figure 1.
Study flow diagram.
Included studies
One randomised clinical trial met inclusion criteria (Hyttel‐Sorensen 2015a). See Characteristics of included studies table.
Hyttel‐Sorensen 2015a was a multi‐centre trial enrolling infants of less than 28 weeks' gestation with no major congenital malformations and a decision to provide full life support. One hundred and sixty‐six infants were randomised to start continuous cerebral NIRS monitoring less than 3 hours after birth until 72 hours after birth versus conventional monitoring plus blinded NIRS. In the experimental group, the treatment was adjusted according to a specific guideline recommending interventions to keep the cerebral oxygenation rStO₂ within the 55% to 85% range. The control were NIRS‐monitored, but the rStO₂ results were blinded to the clinical staff. Two different NIRS instruments were used: INVOS 5100 with an adult sensor (Covidien, Boulder, CO, USA); and NIRO 200NX (Hamamatsu Phototonics, Hamamatsu City, Japan).
The treatment guideline of the study has been described in detail elsewhere (Pellicer 2013). In short, it constitutes a non‐prioritised list of possible interventions to normalise an out‐of‐normal range rStO₂. Basically it suggests that the clinician assess the respiratory, cardiovascular, haemoglobin and blood glucose status, when hypoxia or hyperoxia occurs. The guideline emphasises that all parameters, such as blood pressure and SpO₂, should be kept within normal ranges; but if for example the pCO₂ is low in the normal range, measures to increase the pCO₂ could be a means to increase a rStO₂ in the hypoxic range.
The primary outcome was the duration and extent of rStO₂ outside the target range. This 'burden of hypo‐ and hyperoxia' in %hours was lower in the experimental group (36.1 %hours vs 81.3 %hours, P < 0.0001).
Secondary outcomes included all‐cause mortality at term‐equivalent age, electrical activity of the brain estimated by electroencephalography (EEG), and a brain injury score determined by ultrasonography at ages 1, 4, 7, 14, and 35 days and at term equivalent age. This brain injury score was based on the occurrence and severity of intracranial haemorrhages, white matter abnormalities, ventricular dilation, and cerebral atrophy.
A two‐year follow‐up is planned (Hyttel‐Sorensen 2013b).
Excluded studies
Risk of bias in included studies
Due to the nature of the intervention it is not possible to blind the clinical staff to the group allocation. It is in that respect important that all other potential sources of bias are handled in a rational manner, reducing the risk of systematic errors to a minimum.
Allocation
Hyttel‐Sorensen 2015a reported adequate randomisation and allocation concealment.
Blinding
Hyttel‐Sorensen 2015a had a high risk of performance bias as the group allocation was evident to the personnel and parents. There was, however, a low risk of detection bias as all outcomes were assessed without knowledge of the allocated interventions.
Incomplete outcome data
Hyttel‐Sorensen 2015a reported that two infants in the control group did not have NIRS data recorded; one due to withdrawal of consent and the other due to technical problems. All other data were recorded per protocol and the risk of attrition bias is thus estimated to be low.
Selective reporting
Hyttel‐Sorensen 2015a refers to publication of the protocol: Hyttel‐Sorensen 2013b. All outcomes are per‐protocol, albeit the blood biomarkers and electroencephalography are published elsewhere (Plomgaard 2016).
Other potential sources of bias
Hyttel‐Sorensen 2015a had no other apparent sources of bias, including no interim analyses.
Effects of interventions
We identified only one RCT, thus the data synthesis including TSA described above was not feasible due to too small information sizes. It is important to stress that TSA‐adjusted confidence intervals would be much wider than the intervals presented below. We downgraded the quality of the evidence on all outcomes due to impression (few participants), lack of blinding, and surrogate outcomes (outcomes not directly related to long‐term patient‐important outcomes). All outcomes were rated low or very low quality of evidence according to the GRADE system.
Primary outcomes
Hyttel‐Sorensen 2015a reported no significant difference in mortality until term equivalent age (RR 0.50, 95% CI 0.29 to 1.00; one trial; 166 participants; low quality of the evidence). There are no data available on first‐year mortality, major neurodevelopmental disability, or blindness.
Secondary outcomes
Use of interventions
Hyttel‐Sorensen 2015a reported selected interventions and physiological variables during the intervention period of first 72 hours of life. They did not test these differences between the groups statistically. The following RRs are unadjusted estimates. Number of fluid boluses during the intervention period was similar in the two groups (MD −0.30, 95% CI −0.79 to 0.19; one trial; 166 participants; very low quality of evidence), as was number of infants receiving any blood transfusion (RR 0.83, 95% CI 0.52 to 1.31; one trial; 166 participants; very low quality of evidence), and the use of vasopressors/inotropes (RR 0.98, 95% CI 0.57 to 1.70; one trial; 166 participants; very low quality of evidence). Treatment of a patent ductus arteriosus was more common in the experimental group (RR 2.98, 95% CI 1.14 to 7.75; one trial; 166 participants; very low quality of evidence). Changes in mean airway pressure, inspiratory oxygen fraction, and ventilation were not reported.
Morbidities
Hyttel‐Sorensen 2015a did not report specifically on intraventricular haemorrhage and patent ductus arteriosus. The numbers presented here are retrieved post‐hoc and the RRs on these outcomes are unadjusted. There were no differences in intraventricular haemorrhages: all grades (RR 0.93, 95% CI 0.65 to 1.34; one trial; 166 participants; very low quality of evidence); grade III/IV (RR 0.57, 95% CI 0.25 to 1.31; one trial; 166 participants; very low quality of evidence), whereas cystic periventricular leukomalacia did not occur in either group. Likewise, the SafeBoosC investigators found no significant differences in the occurrence of a patent ductus arteriosus (RR 1.96, 95% CI 0.94 to 4.08; one trial; 166 participants; very low quality of evidence), chronic lung disease (RR 1.27, 95% CI 0.94 to 1.50; one trial; 166 participants; very low quality of evidence), necrotising enterocolitis (RR 0.83, 95% CI 0.33 to 1.94; one trial; 166 participants; very low quality of evidence), and retinopathy of prematurity (RR 1.64, 95% CI 0.75 to 3.00; one trial; 166 participants; very low quality of evidence). They did not collect data on renal impairment or air leaks.
The post hoc data retrieval was performed by the SafeBoosC group, including three of the authors of this review (SHS, CG, GG).
Adverse events
Hyttel‐Sorensen 2015a reported no serious adverse events. They found significantly more skin marks from the NIRS sensor in the control group (RR 0.31, 95% CI 0.10 to 0.92 (unadjusted RR); one trial; 166 participants; very low quality of evidence).
Discussion
Summary of main results
The single randomised clinical trial on cerebral NIRS together with a treatment guideline included in this review, enrolling 166 infants born before 28 weeks of gestation, was designed and powered to explore differences in cerebral oxygenation rather than clinical outcomes. Although a significant reduction in cerebral oxygenation out of normal range was seen in the experimental group, no consistent differences were reported in neonatal morbidities or mortality at term equivalent age. The accrued information size, 166 participants, is too small to do Trial Sequential Analysis. The results of the two‐year neurodevelopmental follow‐up is still pending.
Overall completeness and applicability of evidence
The findings of this review show that the current evidence is inadequate to either support or refute the use of NIRS monitoring in preterm infants.
A single trial not powered to detect clinical differences did suggest that it is possible to stabilise the oxygenation of the brain tissue (Hyttel‐Sorensen 2015a). How this translates into patient‐relevant outcomes is uncertain and the trends toward reduced mortality and less severe brain injury in the trial should be interpreted with great caution. The differences could be by chance; and over‐enthusiasm after early trials have on numerous occasions later proved to be unfounded (Ioannidis 2005). Perhaps the most prominent example was the trial by Rivers and colleagues showing a significant reduction in mortality by early goal‐directed therapy in severe sepsis and septic shock, a result that could not be reproduced in three subsequent major RCTs (Rivers 2001).
The combination of NIRS monitoring and a treatment guideline is complex intervention. However, the only documented difference in treatment between the two groups was medical or surgical closure of patent ductus arteriosus. The data regarding the association between a patent ductus and cerebral rStO₂ are conflicting (Lemmers 2008; Petrova 2011), and it remains to be determined whether treatment of a patent ductus is beneficial (Benitz 2012). It seems unlikely that the difference in treatment of a patent ductus alone could drive the difference in cerebral oxygenation between the two groups. One could suspect that more readily available interventions in the treatment guideline, such as adjusting the FiO₂ or the respiratory rate on the ventilator, were less meticulously documented. Lastly, the result was achieved with two commercial NIRS instruments, INVOS 5100 and NIRO 200NX, with similar device‐specific rStO₂ normal ranges of 55% to 85%: we do not know how this extrapolates to different instrumentation. It is thus important to stress that larger trials are needed as the available evidence cannot stand alone.
The only other randomised clinical trial addressing cerebral NIRS oximetry in preterm infants is Pichler 2016, that examines the feasibility of reducing the burden of cerebral hypoxia and hyperoxia outside the target range during the immediate transition in preterm infants. The intervention period was restricted to the first 15 minutes of life and the cerebral NIRS oximetry was used to guide supplemental oxygen therapy when the pulse oximeter reading was within normal range, but rStO₂ was not. They found that the burden of hypoxia was reduced by providing extra oxygen, but saw no clinically relevant differences in outcomes.
Pichler 2016 is not eligible for this review as we only included trials with more than 24 hours of NIRS monitoring.
There were no serious adverse effects of the NIRS monitoring, but 16 infants had skin marks after the 72 hours of monitoring. This is not surprising as it is well known from pulse oximetry that local skin damage can occur from the sensor and the heat generated. What remains to be determined is if NIRS together with the treatment guideline may result in deleterious interventions. To identify such adverse effects will take a larger trial adequately powered to detect differences in morbidities and mortality.
Quality of the evidence
Considering it is impossible to blind the clinical staff and parents to the intervention, the study included in this review was of adequate methodology and reported outcomes prespecified in the protocol. However, the overall quality of the evidence provided by the meta‐analyses using the GRADE approach for each outcome was assessed as low to very low. As mentioned, the lack of blinding creates an inherent risk of bias; moreover the small sample size causes possible imprecision of effect estimates, and the surrogate outcomes are indirectly linked to the patient‐relevant long‐term outcomes.
We decided post hoc not to conduct the Trial Sequential Analyses, as we were quite far from the required information sizes for the different comparisons. This makes both the Trial Sequential Analysis figures hard to understand and hampers the calculation of Trial Sequential Analysis‐adjusted CI. Therefore, our presented naive 95% CI should be regarded as too optimistic and likely misleading. In future updates, we shall take multiplicity issues into consideration as stipulated in our protocol according to Jakobsen 2014 and Jakobsen 2016.
Potential biases in the review process
The review has been performed by part of the research team who conducted the only eligible study.
We selected to focus on randomised clinical trials and quasi‐randomised studies. These selections are bound to make us focus most on benefits, as randomised trials and quasi‐randomised studies are known to report harms less well (Ioannidis 2009). If we eventually find significant and clinically relevant benefits of NIRS on patient‐centred outcomes, then we will need to conduct a systematic review on harms based on all observational studies.
Agreements and disagreements with other studies or reviews
We have found no other reviews considering the potential benefits and harms of cerebral NIRS oximetry in preterm infants.
| Cerebral NIRS oximetry compared to no cerebral NIRS oximetry in very preterm infants | ||||||
| Patient or population: prevention of morbidities in very preterm infants | ||||||
| Outcomes | Anticipated absolute effects* (95% CI) | Relative effect | № of participants | Quality of the evidence | Comments | |
| Risk with control | Risk with Cerebral NIRS oximetry | |||||
| All‐cause mortality | Study population | RR 0.50 | 166 | ⊕⊕⊝⊝ | ||
| 250 per 1000 | 125 per 1000 | |||||
| Intraventricular haemorrhage grade III or IV | Study population | RR 0.57 | 166 | ⊕⊝⊝⊝ | ||
| 163 per 1000 | 93 per 1000 | |||||
| Cystic periventricular leukomalacia (diagnosed by cranial ultrasound) | Study population | not estimable | 166 | ⊕⊝⊝⊝ | ||
| 0 per 1000 | 0 per 1000 | |||||
| Patent ductus arteriosus | Study population | RR 1.96 | 166 | ⊕⊝⊝⊝ | ||
| 113 per 1000 | 221 per 1000 | |||||
| Chronic lung disease (oxygen supplementation at 36 weeks' postmenstrual age) | Study population | RR 1.27 | 132 | ⊕⊝⊝⊝ | ||
| 467 per 1000 | 593 per 1000 | |||||
| Proven necrotising enterocolitis (Bell's stage II or III) | Study population | RR 0.83 | 166 | ⊕⊝⊝⊝ | ||
| 125 per 1000 | 104 per 1000 | |||||
| Retinopathy of prematurity, any or severe (stage ≥ III) | Study population | RR 1.64 | 166 | ⊕⊝⊝⊝ | ||
| 100 per 1000 | 164 per 1000 | |||||
| Other adverse effects | Study population | not estimable | 166 | ⊕⊝⊝⊝ | ||
| 0 per 1000 | 0 per 1000 | |||||
| *The risk in the intervention group (and its 95% CI) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1 Optimal information size not met. 2 Treatment group allocation not blinded. 3 Surrogate outcome close in the causal pathway to patient‐important outcomes. 4 Surrogate outcome far removed in the causal pathway from patient‐important outcomes. | ||||||
