Acute respiratory distress syndrome (ARDS) and acute lung injury (ALI) are often referred to as acute hypoxemic respiratory failure (AHRF) and are characterized by an inflammatory process of the alveolar– capillary membrane that may arise from a primary lung disease or is secondary to a number of systemic disease processes.1 AHRF results in intrapulmonary shunting with hypoxemia and pulmonary hypertension. Associated hypoxemia is mainly due to a ventilation–perfusion mismatch, resulting in increased intrapulmonary shunting due to pulmonary vasodilation in nonventilated lung regions and vasoconstriction in ventilated areas as well as pulmonary hypertension.2
Nitric oxide (NO) is a potent endogenous vasodilator that can be administered via inhalation. Inhaled NO (iNO) can provide selective pulmonary vasodilatation in well-ventilated lung units, improve ventilation–perfusion mismatch, and subsequently reduce the elevated pulmonary vascular resistance and pulmonary hypertension seen in ARDS.3,4 NO is involved in both the production of and protection from oxidative injury, and is believed to regulate both immune and inflammatory responses.5,6 Two systematic reviews indicated lack of evidence for NO on clinical outcomes and increased risk of adverse effects, e.g., renal dysfunction.4,7,8
The objective of this review was to systematically evaluate the benefits and harms of iNO for adults and children with AHRF, considering the risks of systematic errors (bias) and random errors (play of chance).
To quantify the estimated effect of iNO, we conducted meta-anlyses using the Cochrane Collaboration methodology,9 trial sequential analyses (TSA),10 the GRADE,11 and PRISMA guidelines12 when conducting this systematic review. A thorough protocol and a copublication is published in the Cochrane library.13
We searched the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, and EMBASE up to February 2010 (Appendix 1, see Supplemental Digital Content 1, https://links.lww.com/AA/A219).13 We included all randomized clinical trials. We hand-searched reference lists, reviews, and contacted authors and experts for additional trials. We searched ClinicalTrials.gov, Centre Watch Clinical Trials Listing Service, and ControlledTrials.com for missed, unreported, or ongoing trials.
We included patients with ARDS or ALI according to the various definitions present in the literature. We chose to accept the term standard treatment of ARDS and critically ill patients as reported by many authors, despite the ongoing controversy. We excluded neonates because of the different pathophysiology, treatment, and prognosis.
Data Selection and Extraction
AA screened the titles and abstracts for relevant studies. AA and JB independently extracted data from the retrieved trials. Disagreements were resolved by discussion with JW. Trial authors were contacted for additional information. We evaluated the validity and design characteristics of each trial and bias risk components (random sequence generation, allocation concealment, blinding, incomplete data outcomes, selective outcome reporting, sample size and power calculation, and the ability to perform intention to treat [ITT] analysis) (Appendix 2, see Supplemental Digital Content 2, https://links.lww.com/AA/A220).9 Trials were defined as having a low risk of bias if they fulfilled the above criteria. Our primary end point was mortality at days 28 to 30 and at the longest follow-up. Secondary outcomes included duration of mechanical ventilation, ventilator-free days, partial pressure of arterial oxygen/fraction of inspired oxygen (PaO2/FIO2 ratio), oxygenation index (OI), length of stay in intensive care unit (ICU) and hospital, and adverse events (such as bleeding and renal dysfunction).
Data were summarized as relative risks (RR) with 95% confidence intervals (CI) for dichotomous variables and the mean difference for continuous outcomes. We used random and fixed-effects models for all meta-analyses.14,15 Heterogeneity was explored by visual inspection of the forest plots and by using a standard Cochran's Q2 test and I2. I2 values of 50% and more indicate a substantial level of heterogeneity.9 In the case of heterogeneity (I2 > 10%), we reported results from the random effects model. We analyzed data by ITT and included all patients. All forest plots and meta-analytic estimates were calculated with RevMan 5 (Copenhagen: The Nordic Cochrane Centre, The Cochrane Collaboration, 2008).16
We performed subgroup analyses to assess specific benefits or harms of iNO among pediatric or adult populations on the basis of the duration of drug administration and on the basis of primary versus secondary lung injury. If analyses of various subgroups with binary data were significant, we performed a test of interaction.16,17 We considered P < 0.05 as indicating significant interaction between the iNO effect on mortality and the subgroup category.9
We compared estimates of the pooled intervention effect in trials on the basis of American European Consensus Conference (AECC) criteria for ARDS and ALI versus other definitions, in trials with low risk of bias versus trials with high risk of bias and the effect of different components of risk of bias on the intervention effect.
When possible in trials with 2 or more iNO groups receiving different doses, we combined data for the primary and secondary outcomes3,18,19 due to lack of a consistent dose–response relationship for oxygenation variables.7
To assess publication bias and other types of bias, we created funnel plots for mortality.20
Trial Sequential Analysis
Meta-analyses may result in type I errors due to an increased risk of random error when few data are collected and due to repeated significance testing when updating with new trials.10,21 To assess the risk of type I errors, we used TSA. TSA combines information-size estimation for meta-analysis (cumulated sample size of included trials) with an adjusted threshold for statistical significance in the cumulative meta-analysis.10,21,22 The latter, called trial sequential monitoring boundaries, reduce type I errors. In TSA, the addition of each trial in a cumulative meta-analysis is regarded as an interim meta-analysis and helps to clarify whether additional trials are needed. The idea in TSA is that if the cumulative z curve crosses the trial sequential monitoring boundary, a sufficient level of evidence has been reached and no further trials are needed. If the z curve does not cross the boundary and the required information size has not been reached, there is insufficient evidence to reach a conclusion.10,21,23–25 We applied TSA to reduce the risk of type I error to estimate how many more patients might be needed in further trials.
We summarized the evidence applying GRADE levels11 (high, moderate, low, and very low) by evaluating design, quality, consistency, precision, directness and possible publication bias of the included trials using GRADE pro-version 3.2.2 software.26
Through electronic searches and from references, we identified 1876 publications on iNO. We excluded 1852 duplicates or clearly irrelevant publications. Twenty-four relevant publications were retrieved for further assessment. From these, we included 14 trials that were described in 16 publications and randomized a total of 1303 participants (Fig. 1). We found no ongoing trials. We obtained additional data from 5 authors19,27–30 and from the corresponding author of 1 systematic review.7
The ARDS definition based on the AECC statement was used in all included trials except 3.27,28,30 However, 4 trials applied various other definitions, such as the Murray Lung Injury Score >2.5,32 OI criteria,33 and modified ALI classification.18,34 Two studies were published in abstract form.30,35 Data from 2 trials were distributed in 4 articles.31,33,36,37 Mortality was reported in all studies except 1.35
Characteristics of Included Trials
We included 3 pediatric trials18,28,33: 1 trial enrolled few children,38 and the remaining trials consisted of mixed populations of critically ill adults with ALI and ARDS. The sample size varied from 14 to 385 participants (Table 1).
The duration of iNO varied from <24 hours to 4 weeks with a median length of 7 days. Follow-up ranged from 24 hours to 1 year. In 4 trials the comparison group received nitrogen as placebo3,30,31,35 and air in 1 trial.33 Eight trials applied a fixed dose of iNO (median 10 parts per million [ppm]; range 5 to 10 ppm).18,19,28,30,31,33,35,39 Five trials used the lowest dose to achieve an oxygenation response,27,29,32,34,38 and 1 trial used different doses of iNO.3 Two trials enrolled only iNO responders.27,34
In 5 trials, a few patients allocated to the control group crossed over to iNO as rescue therapy after randomization, according to predefined protocols.30,33–35,38 In 1 trial, all patients received iNO after 24 hours, irrespective of initial allocation.28 We report only mortality data before this cross-over. iNO was either discontinued at the clinician's discretion,35 tapered after a prespecified time period,18,33,38 or tapered after reaching the predefined gas exchange end points.3,27,28–30,34,38 Various cointerventions were applied, such as recruitment maneuver,19 prone position,18,31,39 and corticosteroids.3
Five unblinded trials18,19,27,32,39 and 1 blinded trial used predefined protocols for mechanical ventilation,35 and 3 unblinded trials adhered to guidelines.3,31,33
Characteristics of Included Trials and Assessment of Risk of Bias (Systematic Errors)
Four trials were classified as low bias risk trials (Appendix 2, see Supplemental Digital Content 2, https://links.lww.com/AA/A220).3,30,31,33 Random sequence generation was adequately reported in 7 trials,3,27,29–31,33,34 as was allocation concealment.3,30,31,33–35,39 Five trials were categorized as double-blind.3,30,31,33,35 There was complete mortality follow-up in all trials except 2,35,36 but some of the trials did not provide the exact length of the follow-up (Table 1). Six trials performed ITT analyses of data or provided sufficient data to perform ITT analyses.3,30–32,34,39 Six trials were partly or fully sponsored by industry,3,27,29,31,34,38 1 trial did not disclose funding source,18,19 and the rest of the trials were defined as not for profit. Sample size calculation was reported in 7 trials,3,27,29–31,34,38,39 but only 2 were powered to show a statistically significant benefit in primary end points.31,34 However, 1 of these studies34 was stopped early because of slow enrollment (45% of sample size), and the other31 only enrolled 75% of the planned sample size, for unknown reasons. The funnel plot showed a symmetrical distribution that indicated no publication bias (Appendix 3, see Supplemental Digital Content 3, https://links.lww.com/AA/A221).
Combining data from 14 trials the longest follow-up showed no statistically significant effect of iNO on mortality: 265out of 660 deaths (40.2%) in the iNO group in comparison with 228out of 590 deaths (38.6%) in the control group (RR 1.06, 95% CI 0.93 to 1.22; I2 = 0%, Fig. 2). The 28-day mortality analysis showed 36% (208out of 578) deaths in the iNO group and 32.7% deaths (165out of 504) in the control group (RR 1.12, 95% CI 0.95 to 1.31; I2 = 0%, Fig. 3). Median duration of intervention was longer than 1 week in 8 trials.3,19,27,29,31,32,34,39 We did not identify any significant effects of iNO in any of the prespecified subgroups. We did not conduct a subgroup analysis assessing the effect of different iNO dosages because there does not appear to be any evidence to support this7 and many trials did not use a fixed dose of iNO but applied dose titration.
There was no beneficial effect of iNO on ventilator-free days or the duration of mechanical ventilation (Table 2). The PaO2/FIO2 ratio was statistically improved at 24- and 96-hour analyses favoring iNO3,29,34,39 but with no significant differences in the 48- and 72-hour analyses (Table 2).
The OI was significantly lower in the iNO group at 24, 72, and 96 hours but not at the 48-hour analysis (Fig. 3, Table 2). Additionally, the rate of severe respiratory failure decreased in the iNO group (RR 0.21, 95% CI 0.05 to 0.79; I2 = 0).27,34 Two trials27,34 provided data on reversal of ALI, with no statistically beneficial effect of iNO. Differences in mean pulmonary arterial pressure was initially significant at day 13,19,28,29,39 but no longer present on days 2, 3, or 4 (Table 2).
All trials assessed methemoglobin concentrations. Four patients in the iNO group and 3 patients in the control group had methemoglobin values >5%. Data on nitrogen dioxide was reported in 8 trials3,18,27,29–31,33,39 but only 1 trial31 reported patients with increased concentrations; all had received 80 ppm iNO. iNO increased the risk of renal impairment on the basis of data from 4 trials (RR 1.59, 95% CI 1.17 to 2.16; I2 = 0%, Fig. 4). We accepted the various definitions of renal impairment (Appendix 4, see Supplemental Digital Content 4, https://links.lww.com/AA/A222), although application of a uniform classification such as RIFLE could potentially have increased the validity of our results. A sensitivity analysis excluding the trial with highest event rate did not change the overall picture, indicating a persistent harmful effect (RR 1.79, 95% CI 1.16 to 2.77; I2 = 0%). Other adverse events were variably reported and did not reach statistical significance. Finally, there was no significant increase in bleeding events.3,29,30,34,38
Resolution of Multiorgan Failure, Quality of Life and Cost–Benefit Analysis
One trial reported on resolution of multiorgan failure (Therapeutic Intervention Scoring System [TISS] score), with no statistically beneficial effect.31 One trial assessed quality of life36 with no statistically significant effects. Data for cost–benefit analysis and length of stay in hospital and in the ICU was provided by only 1 trial. There was no indication of reduced stay in the ICU or hospital31 with similar hospital costs of $48,500 US in the iNO group versus $47,800 US in the control group (P = 0.8).36
To detect or reject an a priori intervention effect of 10% RR reduction (RRR), we needed 4679 participants to provide the information size. Only 26% of this number was randomized with no boundaries crossed (Fig. 5). The intervention effect suggested by the trials with low risk of bias, in the meta-analysis of the effect of iNO on mortality, was an RR increase (RRI) of 3.85%. The low-bias heterogeneity-adjusted information size calculated on the basis of this intervention effect is 36,107 participants. Thus, only 3% of the required information size is actually available to reject or accept a 3.85% RRI or RRR of mortality. The TSA of PaO2/FIO2 ratio at 24 hours did, however, indicate statistical significance in favor of improved oxygenation, because the z curve crossed the trial sequential monitoring boundary (Fig. 6).
Summary of Evidence According to GRADE
As is indicated above, there were variable risks of bias in a majority of the trials, leading us to downgrade the quality of the evidence. Our application of GRADE methodology led us to conclude that the accumulated evidence is of low to moderate quality (Appendix 5, see Supplemental Digital Content 5, https://links.lww.com/AA/A223).
In this systematic review of 14 trials with 1303 patients with ALI and ARDS, we found no benefits of iNO on survival. The analysis on mortality showed no heterogeneity and was robust when performing different subgroup and sensitivity analyses. Conversely, iNO increased the risk of renal failure. It transiently improved oxygenation, only for the first 24 hours. The sparse data on mortality are not promising but are not evidence of the absence of a beneficial effect; the data suggest that a potentially beneficial effect of iNO must be modest, and the current point estimate suggests harm.
We did not find any statistically significant difference when examining the effects in subgroups according to duration of intervention, intervention among different populations (pediatrics, adults), and sensitivity analysis excluding trials published only as abstracts. The 3 pediatric trials with 162 patients were insufficient to demonstrate any benefits or harms of iNO therapy in pediatric ALI and ARDS.
Subgroup and sensitivity analyses assessing the impact of varied primary etiologies, reversal of ALI resolution of multiorgan failure, quality-of-life assessment and bias assessment did not result in statistically significant findings. Additional analyses such as adverse events indicated an increased risk of renal failure among adults, whereas there were no signs of increased risk of bleeding, methemoglobinemia, or increased nitrogen dioxide concentration except possibly among patients receiving iNO doses above 80 ppm. Outcomes such as duration of stay, in both the ICU and hospital, and other clinically relevant outcomes were inconsistently reported. Authors were contacted for missing data. Few responded and did not provide much additional information.
Despite evidence of an initial but transient improved oxygenation in the iNO group, these analyses were limited because of application of different indicators of oxygenation, different time points for oxygenation measurement, and demonstration of a therapeutic effect in graphic form without adjacent numerical data in most publications, thus preventing adequate pooling of data.
Even though a beneficial effect is true, oxygenation is only a surrogate outcome, and it is uncertain whether it predicts any clinical benefits. Additionally, many trials were conducted before the general recommendation of the lung-protective, low tidal volume ventilation strategy40 and application of high positive end-expiratory pressure among ARDS patients.41 The latter combined with oxygen toxicity, surfactant inhibition, and ongoing fibrosis as a result of ARDS may have biased the results of these trials. The amount of sedatives and muscle relaxants used and the use of protocolized weaning could also potentially play a role. However, because there was no difference in the mode of ventilation and overall treatment between the iNO and control groups, this should not account for our findings of lack of benefit on survival and in potential harm.
There are several theoretical explanations for why iNO may not be beneficial. Reversal of the hypoxic pulmonary vasoconstriction could cause vasodilatation of poorly ventilated areas, increasing the ventilation–perfusion mismatch and resulting in worsening oxygenation.42 Additionally, prolonged exposure to iNO and its toxic metabolites could cause sensitization and override the possible benefits of iNO.39 Improved oxygenation is not associated with increased survival because improved oxygenation does not necessarily indicate improved lung function, reduction of lung injury, or resolution of the underlying cause of ARDS and the often coexisting multiorgan failure.43,44 NO is an important regulator of renal vascular tone and a modulator of glomerular function. Changes in NO production could potentially cause acute renal failure by altering the function of mitochondria, various enzymes, DNA, and membranes.7,45
TSA confirm that there is a lack of firm evidence for a beneficial effect with a 3.85% RR increase. Additionally, there is insufficient information size to reject the anticipated intervention effect, and that a substantial number of patients might be needed to identify a possibly beneficial effect.
Strengths and Limitations
We used a comprehensive search strategy, evaluated systemic and random errors and incorporated GRADE classification. Our findings and interpretations are limited by the quality and quantity of available evidence. The risk of bias of the included trials was mainly assessed by using the published data, which ultimately may not reflect the truth. All authors were contacted, but only a few responded and provided further information. Many of our analyses were limited because most of the studies demonstrated a therapeutic effect in graphic form, without numerical data in the publications. Additionally, several clinical outcome variables in line with our defined primary and secondary outcomes were inconsistently reported. We were unable to retrieve protocols of the published trials and thus were unable to compare the published outcomes to the proposed outcomes in the protocols.
There was minimal heterogeneity among trial results on mortality, but we are aware that we pooled heterogeneous trials in terms of age, patients, settings, and treatment regimens. Thus, the validity of our meta-analysis may be criticized. However, all trials included patients with acute respiratory failure with similar inflammatory pathways. Therefore, we think that there is a good biologic reason to perform a broad meta-analysis, which also considerably increases the generalizability and usefulness of the review.
There is insufficient evidence to support the use of iNO in any category of ARDS and ALI patients. We did not find a statistically significant effect of iNO on mortality or other clinical outcomes except signs of improved oxygenation, and the current results are not promising. iNO appeared to increase the risk of renal failure. We believe that iNO should only be used as part of randomized clinical trials. Future trials need to focus on other relevant clinical outcomes.
Name: Arash Afshari, MD.
Contribution: See Appendix 7, Supplemental Digital Content 7, https://links.lww.com/AA/A225.
Name: Jesper Brok, MD, PhD.
Contribution: See Appendix 7, Supplemental Digital Content 7, https://links.lww.com/AA/A225.
Name: Ann M. Møller, MD, MSDC.
Contribution: See Appendix 7, Supplemental Digital Content 7, https://links.lww.com/AA/A225.
Name: Jørn Wetterslev, MD, PhD.
Contribution: See Appendix 7, Supplemental Digital Content 7, https://links.lww.com/AA/A225.
We would like to acknowledge Drs. Sokol, Jacobs, and Bohn's work on the original review.4,9 We would like to thank Dr. Karen Hovhannisyan for his assistance in providing our different search strategies and search results and by facilitating contact to various authors. We would like to thank Jane Cracknell for her extensive support. Special thanks to Dr. Neill Adhikari for his valuable data on iNO treatment in various trials and on various outcomes on behalf of several lead authors of the included studies. Additionally, we would like to thank Dr. R. Scott Watson, Dr. Peter Dahlem, Dr. Harald Herkner, and Dr. Nathan L. Pace for their insightful and valuable criticism, enabling us to improve the overall quality of this paper.
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