Description of studies
See: Characteristics of included studies; Characteristics of excluded studies.
Nineteen studies were found to be eligible for inclusion in this review. Thirty-two additional studies were initially identified as possibly eligible but were excluded. For each trial included in the review, clinical details concerning the participants, interventions and outcomes are given in the table, Characteristics of Included Studies.
Twelve of the 19 identified studies were conducted within the United States of America. The others were conducted in Argentina [Gutierrez 1987], the United Kingdom [Rennie 1986a], Canada [Vincer 1985], Mexico [Gutierrez 1987], Thailand [Supapannachart 1999], Saudi Arabia [Yaseen 1997] and by an international collaboration involving Canada, USA, Australia, New Zealand and Hong Kong [TIPP 2001].
Clinical practices (cointerventions) would be expected to vary across centres and over time in the studies included in this review. However, when the studies were appropriately randomised and blinded, this only becomes an issue when generalising results. Two specific issues are worth noting however. The study reported by Gutierrez et al [Gutierrez 1987] took place in a unit that did not ventilate babies whereas assisted ventilation was offered in all other studies. Surfactant usage has increased over time and was given either as prophylaxis or rescue therapy in seven trials (Couser 1996, Domanico 1994, Ment 1994a, Ment 1994b, Supapannachart 1999, TIPP 2001, Yaseen 1997).
The size of the individual studies ranged from single centre studies enrolling less than 50 patients, [Bandstra 1988, Krueger 1987, Ment 1985, Puckett 1985 and Vincer 1985] to the international multicentre study (TIPP 2001) which enrolled over 1200 babies.
All babies were less than 37 weeks and most studies had an upper gestational age limit (or equivalent weight limit) for inclusion of less than this.
Bada 1989, Hanigan 1988, Krueger 1987, Ment 1985, Ment 1988, Ment 1994b; Morales-Suarez 1994 and Rennie 1986a performed cranial ultrasounds before study entry and excluded infants with intraventricular hemorrhage. Ment 1994a reported the results of a cohort of infants all of whom had grade 1 or 2 IVH on pre-study scan. The remaining studies enrolled infants without knowledge of pre-existing IVH.
All the studies used prophylactic intravenous indomethacin as treatment although the dosage schedules varied enormously from a single dose of 0.2 mg/kg at 24 hours of age [Krueger 1987] to a daily dose of 0.1 mg/kg given for 6 days [Couser 1996]. A placebo was used as control in all studies apart from the study reported by Krueger et al [Krueger 1987]. The placebo was unspecified in four studies, [Bada 1989, Gutierrez 1987, Mahony 1985 and Puckett 1985], with saline being used in the remainder.
The majority of the studies included in the review examined short-term clinical outcomes prior to discharge from hospital. Many of the outcome definitions varied slightly, in particular the definition of chronic lung disease. Several studies looked at a variety of measures pertaining to renal function including urine output and serum biochemistry, but there was little consistency between studies as to which measures and which cut-off points were used. The same difficulty arose when examining haemostasis when the platelet count, bleeding time and "clinical bleeding" were all used but in slightly different ways in different studies. There were relatively few data available examining long-term neurodevelopmental outcome [Bandstra 1988, Couser 1996, Ment 1994b, TIPP 2001, Vincer 1985]. Along with physical and sensory outcomes, two scoring systems are used to report outcome - Bayley scores and Stanford-Binet IQs. As well as reporting these cognitive outcomes separately, a pooled analysis of the outcome "severe developmental delay" was conducted by dichotomising both test results at 2 standard deviations below the mean.
Risk of bias in included studies
For each trial included in the review, assessments of the methodological quality are given in the table, Characteristics of Included Studies.
The methodological details for each study were extracted from the published information only. It may well be, therefore, that some studies were more rigorously conducted than appears from this assessment. This is particularly so of studies where data are still only found in published abstracts [Bada 1989, Domanico 1994 and Puckett 1985]. Although methodological information is limited in the abstract reporting the results of the study by Gutierrez et al [Gutierrez 1987], more details were obtained from the trial registration with the Oxford Database of Perinatal Trials.
The exact method of concealment of randomisation could be determined for twelve of the included studies [Bandstra 1988, Couser 1996, Gutierrez 1987, Hanigan 1988, Mahony 1985, Ment 1985, Ment 1988, Ment 1994a, Ment 1994b, TIPP 2001, Supapannachart 1999 and Yaseen 1997]. Methods included telephone randomisation, sealed envelopes and coded vials. In the remaining seven studies, from the published information, it was not possible to tell how well randomisation was blinded.
Blinding of the intervention to those caring for the infant was explicitly described in nine of the studies [Bandstra 1988, Couser 1996, Domanico 1994, Gutierrez 1987, Hanigan 1988, Mahony 1985, Ment 1985, Ment 1988, Vincer 1985 and TIPP 2001]. In the study reported by Krueger et al [Krueger 1987], it appears that the carer was clearly not blinded to the intervention group. Blinding of the intervention is unclear in the trials of Puckett 1985 and Rennie 1986a.
In three studies, [Krueger 1987, Puckett 1985 and Rennie 1986a], it is not possible to determine whether or not those responsible for assessing the outcomes of interest were blind to intervention group. In all the other studies, blinding was adequate.
For all the short-term outcome measures prior to discharge, follow-up was adequate for all the studies included, in that it was greater than 90%. In contrast, long-term outcome assessment was less complete. If all infants randomised form the denominator, and all infants on whom some follow-up data is available (including death) form the numerator, follow rates were as follows: Bandstra 1988 - 75%, Couser 1996 - 73%, Ment 1994b - 90%, TIPP 2001 - 95% and Vincer 1985 - 100%. For individual long-term outcomes, particularly cognitive testing, follow-up rates were much lower and this is a potential source of bias.
The study of Ment 1994b requires some explanation. Four hundred and thirty one infants were randomised within the study. Forty-five died before hospital discharge and their group of allocation is known. Follow-up testing was conducted at 36 months corrected age and again at 54 months corrected age. At 36 months, 343 were assessed clinically for the presence or absence of cerebral palsy. Fewer were formally assessed for hearing impairment (135) and visual impairment (158). 251 infants underwent objective cognitive function testing. Cognitive function testing was limited to children who spoke English as their first and only language because of concerns that the instruments used, the Stanford-Binet Intelligence Scale and the Peabody Picture Vocabulary - Revised, were not valid in non-English speaking or multilingual children. The proportions of survivors who were tested for cognitive function at follow-up were similar for the indomethacin and placebo groups. However, no data were provided on those children not assessed making it impossible to determine whether all eligible children were tested or whether those not tested might have differed significantly in other ways than ethnic origin to those children who were assessed. At 54-months vision and hearing were assessed in 337 infants, presence or absence of cerebral palsy in 323 and cognitive testing in 233. For the purposes of this review, we used the 54-month outcomes for vision and hearing and the 36-month outcome for cerebral palsy to minimise loss to follow-up.
Bandstra et al report neurodevelopmental follow-up on 123 of the 199 infants (28 deaths) enrolled in their study [Bandstra 1988]. The results are available in an abstract only and more complete data do not appear to have been published. This leads to two obvious problems: (1) the data refer to a selected subset of the trial population i.e. those who, at the time of writing the abstract, had turned up for review; and (2) it appears that the MDI and PDI scores were assessed at 6, 12, 18 and 24 months but the data for each individual infant refer to the most recent test for that infant. It may not be appropriate to compare results between infants when the scores were assessed at different times. This may lead to a biased result, and caution is needed in interpreting these results.
Effects of interventions
Nineteen studies contributed data to the review.
There is no statistically significant difference in neonatal mortality between the treatment and placebo groups. However, the 95% confidence interval around the pooled estimate suggests a trend toward a reduction in the early mortality rate in those infants treated with prophylactic indomethacin, pooled relative risk (RR) = 0.82 [95% CI 0.65 to 1.03]. However, when the outcome "death at latest follow-up" is examined a trend favouring prophylactic indomethacin is no longer apparent [RR = 0.96 (0.81,1.12)]. The difference in these results appears to be due to the contribution of TIPP 2001 to the latter outcome and the absence of data from TIPP 2001 on mortality before hospital discharge.
Patent ductus arteriosus.
Prophylactic indomethacin reduces the incidence of symptomatic patent ductus arteriosus, pooled RR = 0.44 [0.38 to 0.50], pooled risk difference (RD) = -0.24 (-0.28 to -0.21), number needed to treat (NNT) = 4. The incidence of echo-diagnosed patent ductus arteriosus, i.e., the sum of all patent ductuses whether symptomatic or not, is reduced even further by prophylactic indomethacin [RR = 0.29 [0.22 to 0.38], RD = -0.27 (-0.32,-0.21), NNT = 4]. Prophylactic indomethacin reduces the rate of surgical PDA ligation [RR = 0.51, (0.37,0.71), RD = -0.05 (-0.08, -0.03), NNT = 20]
There is no significant difference between treatment and placebo groups as regards any of the pulmonary outcomes examined: pneumothorax, duration of ventilation, duration of supplemental oxygen requirement or incidence of chronic lung disease (defined at either 28 days or 36 weeks). A trend towards reduction in rates of pulmonary haemorrhage in infants randomised to prophylactic indomethacin does not reach statistical significance [RR = 0.84 (0.66,1.08)]
Cranial ultrasound abnormalities:
The incidence of intraventricular haemorrhage of all grades is significantly reduced in infants who receive prophylactic indomethacin [RR = 0.88 (0.80 to 0.98), RD = -0.04 (-0.08,-0.01), NNT= 25]. There is evidence that the treatment effect on this outcome is not consistent across all studies, with statistical heterogeneity detected (p = 0.011) on chi-squared test. An analysis of the trials providing data on Grade 3 and 4 haemorrhage also shows an effect favouring prophylactic indomethacin [RR = 0.66 [0.53 to 0.82], pooled RD = -0.05 (-0.07 to -0.020), NNT = 20]. The reduction in severe IVH is similar whether or not infants were screened for IVH and excluded before study entry. There is no evidence that prophylactic indomethacin prevents the progression of Grade 1 IVH that is present before prophylaxis is commenced, although only two small studies contributed data to this outcome. Pooled results from the five trials reporting outcomes of either periventricular leukomalacia or ischaemic change showed a reduction in rate of adverse outcome in infants treated with prophylactic indomethacin [RR = 0.44 (0.24,0.81), RD = -0.05 (-0.08,-0.01)]. TIPP 2001 reported rates of white matter injury on ultrasound (including intraparenchymal echodensities, periventricular leukomalacia, porencephalic cysts and ventriculomegaly) which showed a trend in the same direction [RR = 0.88 (0.71,1.09), RD = -.03 (-0.08, 0.02)].
Caution should be exercised in the interpretation of these results because of the methodological limitations of some of the studies as mentioned above. The high rates of loss to follow-up for some trials and particularly for long-term cognitive outcomes limit the applicability of some results.
The two studies using Bayley examinations (TIPP 2001 and Bandstra 1988) showed no difference in rates of severe impairment (Mental Developmental Index < 68) [RR = 1.02 (0.83,1.26)]. Ment 1994b using the WIPPSI-R (full scale < 70) at 54 months found a non-significant trend favouring the prophylactic indomethacin group [RR = 0.55 (0.28,1.11)]. Combining these three studies results in no difference between treatment groups for the outcome severe developmental delay [RR = 0.96 (0.79,1.17)].
Ment 1994b also assessed the same cohort at 36 months. Mean Stanford-Binet IQ scores (SD) were not statistically different in the two groups: 89.6 (18.92) for indomethacin, 85.0 (20.79) for placebo, Mean Difference = 4.7 (95% CI -0.703 to 10.103) and there was no difference in Peabody Picture Vocabulary Test - Revised scores: 88.4 (20.01) for indomethacin, 83.7 (21.78) for placebo, Mean Difference = 4.6 (-0.352 to 9.552).
Four studies reporting this outcome showed no difference in rates of cerebral palsy [RR = 1.04 (0.77,1.40)].
There were no significant differences in rates of blindness [RR = 1.26 (0.50,3.18)] or deafness [RR = 1.02 (0.45,2.33)] in the 2 studies reporting these outcomes (Ment 1994b and TIPP 2001).
There was no significant difference in rates of severe neurosensory impairment (CP, cognitive delay, blindness, deafness) [RR = 0.98 (0.81,1.18)] or death or severe neurosensory impairment [RR = 1.02 (0.90,1.15)]. TIPP 2001presented subgroup analyses based on birthweight (500-749g and 750-999g) and there were no significant differences in rates of composite adverse outcomes in either subgroup (indomethacin 63% and 36% vs control 61% and 35%).
There is no significant difference in rates of necrotizing enterocolitis [RR = 1.09 (0.82,1.46)]. The one trial (TIPP 2001) reporting gastrointestinal perforation found no significant difference in rates of this outcome [RR = 1.12 (0.71,1.79)].
The incidence of oliguria is increased in infants who receive prophylactic indomethacin [RR = 1.90 (1.45 to 2.47), RD = 0.06 (0.04,0.08), Number needed to harm = 16]. In two trials, Ment has also reported the number of infants in each group whose creatinine rose above 159 micromol/L. The pooled results show no difference between the groups, in keeping with Couser who found no difference in the number of infants whose creatinine rose beyond 18 mg/dl. Mahony reported mean serum sodium, potassium and creatinine on day three as well as mean urine output over the first four days. There is no statistically significant difference between the groups in any of these measures. Vincer reported mean serum sodium levels over the first seven postnatal days and points to a significantly higher level in the treatment group on days three and four. In addition to reporting reduced urine output in the treatment group, Rennie reported significantly higher peak creatinine levels on days one and two following treatment with indomethacin but no significant difference in serum sodium levels. Krueger reported a significant reduction in urinary output (as measured by the input/output ratio) affecting the treatment group in the 24 hours immediately following treatment. This difference is no longer apparent in the subsequent 24 hour period. In 1988, Ment reported no clinically important renal abnormalities but provides no data. Bada provided data that show statistically significant changes in plasma creatinine and sodium levels, osmolalities and urine output but comments that these differences were not abnormal, i.e. not clinically important.
In three reports, Ment provides data on the number of infants whose platelet count fell to <50,000 per microlitre. Couser found no difference in the number of infants whose platelet count fell below 50,000 per microlitre although platelet counts were not routinely measured, only being estimated at the request of the clinician caring for the infant. The pooled estimate shows no difference in the rates of thrombocytopenia [RR = 0.50 (0.11,2.22)]. Likewise, combining the five trials reporting rates of excessive clinical bleeding shows no difference between the groups [RR = 0.74 (0.40,1.38)]
Retinopathy of prematurity (ROP)
There is no evidence of a significant difference in the rates of any ROP [RR = 1.02 (0.92,1.14)] or severe ROP [RR = 1.75 (0.92,3.34)].
In four trials, the risk of sepsis was not significantly different between groups [RR = 0.78 (0.56,1.09)].