Inhaled nitric oxide for treating pain crises in people with sickle cell disease

Abstract

Background

In people with sickle cell disease, sickled red blood cells cause the occlusion of small blood vessels which presents as episodes of severe pain known as pain crises or vaso‐occlusive crises. The pain can occur in the bones, chest, or other parts of the body, and may last several hours to days. Pain relief during crises includes both pharmacologic and non‐pharmacologic treatments. The efficacy of inhaled nitric oxide in pain crises has been a controversial issue and hypotheses have been made suggesting a beneficial response due to its vasodilator properties. Yet no conclusive evidence has been presented.

This review aims to evaluate the available randomised controlled studies which address this topic.

Objectives

To capture the available body of evidence evaluating the efficacy and safety of the use of inhaled nitric oxide in treating pain crises in people with sickle cell disease; and to assess the treatment's relevance, robustness, and validity, in order to better guide medical practice in the fields of haematology and palliative care (since recent literature seems to favour the involvement of palliative care for those people).

Search methods

We searched the Cochrane Cystic Fibrosis and Genetic Disorders Group's Haemoglobinopathies Trials Register. Unpublished work is identified by searching the abstract books of the European Haematology Association conference; the American Society of Hematology conference; the British Society for Haematology Annual Scientific Meeting; the Caribbean Health Research Council Meetings; and the National Sickle Cell Disease Program Annual Meeting.

Date of most recent search: 19 September 2019.

We also searched ongoing study registries, date of most recent search: 26 September 2019.

Selection criteria

Randomised and quasi‐randomised trials comparing inhaled nitric oxide with placebo, or standardized way of treatment of pain crises in people with sickle cell disease.

Data collection and analysis

Two authors independently assessed trial quality and extracted data (including adverse event data). A third author helped clarify any disagreement. When the data were not reported in the text, we attempted to extract the data from any table or figure available. We contacted trial authors for additional information. We assessed the quality of the evidence using the GRADE criteria

Main results

We identified six trials, three of which (188 participants) were eligible for inclusion in the review. There were equal numbers of males and females; and most participants were adults, although one small trial was conducted in a children's hospital and recruited children over the age of 10 years. All three parallel trials compared inhaled nitric oxygen (80 ppm) to placebo (room air) for four hours; one trial continued administering nitric oxide (40 ppm) for a further four hours. This extended trial had an overall low risk of bias; however, in the remaining two trials we had concerns about the risk of bias from the small sample size and additionally a high risk of bias due to financial conflicts of interest in one of these smaller trials. We were only able to analyse some limited data from the eight‐hour trial and report the remaining results narratively.

The time to pain resolution was only reported in one trial (150 participants), showing there may be little or no difference between the two groups: with inhaled nitric oxide median 73.0 hours (95% confidence interval (CI) 46.0 to 91.0) and with placebo median 65.5 hours (95% CI 48.1 to 84.0) (low‐quality evidence). No trial reported on the duration of the initial pain crisis. Only one large trial reported on the frequency of pain crises in the follow‐up period and found there may be little or no difference between the inhaled nitric oxide and placebo groups for a return to the ED, risk ratio 0.73 (95% CI 0.31 to 1.71) or for re‐hospitalisation, risk ratio 0.53 (95% CI 0.25 to 1.11) (150 participants; low‐quality evidence).

There may be little or no difference between treatment and placebo in terms of reduction in pain score at any time point up to eight hours (150 participants). The two smaller trials reported a beneficial effect of inhaled nitric oxide in reducing the visual analogue pain score after four hours of the intervention, but these trials were small and limited compared to the first trial.

Analgesic use was reported not to differ greatly between the inhaled nitric oxide group and placebo group in any of the three trials, but no analysable data were provided. The median duration of hospitalisation was reported by two trials, in the largest trial the placebo group had the shorter duration and in the second smaller (paediatric) trial hospitalisation was shorter in the treatment group.

Only the largest trial (150 participants) reported serious adverse events, with no increase in the inhaled nitric oxide group during or after the intervention compared to the control group (acute chest syndrome occurred in 5 out of 75 participants from each group, pyrexia in 1 out of 75 participants from each group, dysphagia and a drop in haemoglobin were each reported in 1 out of 75 participants in the inhaled nitric oxide group, but not in the placebo group) (low‐quality evidence).

Authors' conclusions

The currently available trials do not provide sufficient evidence to determine the effects (benefits or harms) of using inhaled nitric oxide to treat pain (vaso‐occlusive) crises in people with sickle cell disease. Large‐scale, long‐term trials are needed to provide more robust data in this area. Patient‐important outcomes (e.g. measures of pain and time to pain resolution and amounts of analgesics used), as well as use of healthcare services should be measured and reported in a standardized form.

Plain language summary

Inhaled nitric oxide for treating pain crises in people with sickle cell disease

Review question

We reviewed the evidence about the effects of inhaled nitric oxide for relieving pain crises in people with sickle cell disease.

Background

Sickle cell disease is a condition that affects the red blood cells. Normal red blood cells are round, but in people with sickle cell disease some of the red blood cells can have an abnormal shape. They look like a crescent (or an old‐time tool called a 'sickle'). The abnormally‐shaped cells easily become stuck in blood vessels which can cause episodes of severe pain called 'pain crises'. The pain can be in the bones, chest, or other parts of the body, and can last from several hours to days.

Painkillers are the main treatment of these pain crises. Another suggested treatment is inhaled nitric oxide, which is a gas that can relax the blocked blood vessels so they can widen and allow the sickled cells to pass. We wanted to evaluate whether inhaled nitric oxide is effective in relieving pain in people with sickle cell disease.

Search date

The evidence is current to: March 2018.

Trial characteristics

The review included three trials with 188 people (equal numbers of males and females) with sickle cell disease who were experiencing a pain crisis. Most participants were adults, except for one trial conducted in a children's hospital where most participants were children over 10 years of age. The trials compared inhaled nitric oxide with a control (room air), which does not provide pain relief, and people were selected for one treatment or the other at random. The treatments in two trials lasted for four hours and in the third trial lasted for eight hours.

Key results

Only one large trial (150 participants) reported no difference in the time until the pain stopped between nitric oxide or room air. This trial was also the only trial to report on the frequency of pain crises in the follow‐up period and we found little or no difference between inhaled nitric oxide and room air for a return to the emergency department or for re‐admission to hospital. All three trials reported pain scores; the larger trial found no difference between nitric oxide or room air at each time‐point up to eight hours, but the two smaller trials (38 participants) reported a benefit of inhaled nitric oxide in relieving the pain after four hours, but these trials were small and limited compared to the first trial.

All three trials reported that inhaled nitric oxide had no effect on decreasing the use of painkillers, but did not provide any data we could analyse. Two trials reported the average duration of stay in hospital; in the large trial those who were given room air had a shorter stay, and one of the smaller trials (at the children's hospital) reported a shorter stay in those treated with inhaled nitric oxide. Only the larger trial reported harmful effects of nitric oxide and found that treatment made little or no difference.

We could not combine the available data from the three included trials due to differences in the reporting of outcomes. Therefore, the currently available evidence is not enough to give a definitive answer about the use of inhaled nitric oxide for people with sickle cell disease experiencing a pain crisis.

Future trials, preferably large‐scale and long‐term, should be carried out to provide strong evidence in this area. Investigators should measure and report outcomes important to patients (e.g. measures of pain and time to pain resolution and amounts of analgesics used) as well as use of healthcare services in a standardised way.

Quality of the evidence

We judged the evidence we were able to analyse to be of low quality. We believe that the the results in this review were affected because not all planned outcomes were reported in two of the trials and the trials were only small. Furthermore, the fact that the pharmaceutical industry financed the smaller adult trial should be considered when looking at the results of this trial.

Summary of findings

for the main comparison.

Inhaled nitric oxide compared with control for pain crises in people with sickle cell disease
Patient or population: adults and children with SCD Settings: inpatient Intervention: iNO Comparison: control
Outcomes	Illustrative comparative risks* (95% CI)		Relative effect (95% CI)	No of Participants (studies)	Quality of the evidence (GRADE)	Comments
	Assumed risk	Corresponding risk
	Control	iNO
Time to pain resolution Follow‐up: 300 hours	The median time to resolution of a pain crises in the control group was 65.5 hours.	The median time to resolution of a pain crises was 7.5 hours higher (46.0 lower to 91.0 higher).		150 (1 study)	⊕⊕⊖⊖ lowa
Frequency of pain crises in the follow‐up period: return to ED Follow‐up: 30 days	150 participants per 1000 returned to the ED within 30 days.	108 participants per 1000 returned to the ED within 30 days (48 to 258).	RR 0.73 (0.31 to 1.71)	150 (1 study)	⊕⊕⊖⊖ lowa	RR less than 1 indicates an advantage for iNO.
Frequency of pain crises in the follow‐up period: re‐hospitalisation Follow‐up: 30 days	230 participants per 1000 were re‐hospitalised within 30 days.	122 participants per 1000 were re‐hospitalised within 30 days (57 to 255).	RR 0.53 (0.25 to 1.11)	150 (1 study)	⊕⊕⊖⊖ lowa	RR less than 1 indicates an advantage for iNO.
Adverse events Follow‐up: end of trial	See comments.		N/A	150 (1 study)	⊕⊕⊖⊖ lowa	The paper reported the following adverse events: acute chest syndrome in 5/75 (6.7%) participants from each group, RR 1.00 (95% CI 0.30 to 3.31); pyrexia 1/75 (1.3%) participants from each group, RR 1.00 (95% CI 0.06 to 15.69); dysphagia in 1/75 participants in the iNO group, RR 3.00 (95% CI 0.12 to 72.49); and a drop in haemoglobin in 1/75 participants in the iNO group, RR 3.00 (95% CI 0.12 to 72.49).
*The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The assumed risk is calculated as the event rate in the control group. The corresponding risk in the inhaled nitric oxide group (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). CI: confidence interval; ED: emergency department; iNO: inhaled nitric oxide; RR: risk ratio; SCD: sickle cell disease.
GRADE Working Group grades of evidence High quality: further research is very unlikely to change our confidence in the estimate of effect. Moderate quality: further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate. Low quality: further research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate. Very low quality: we are very uncertain about the estimate.

^a Downgraded once due to unclear risk of selection bias (no details on how the randomisation sequence was generated and very limited information on allocation concealment), and once for low precision (small numbers of events and wide CIs).

Background

Description of the condition

Sickle cell disease (SCD) is an autosomal recessive disorder of the beta (β) globin gene. Mutant haemoglobin S stiffens the membrane of red blood cells causing an accumulation of rigid cells and the occlusion of small blood vessels. This presents as episodes of severe pain known as vaso‐occlusive crises (VOCs), with damage to vital organs and even early death (Belcher 2005).

Such VOCs are defined as pain episodes related to SCD in the extremities, back, abdomen, chest or head lasting at least two hours and leading to an emergency or a clinic visit or hospitalisation; acute pain is the most common reason for emergency department (ED) visits in people with SCD (Yusuf 2010). VOC pain can begin as early as six months of age and typically lasts throughout life (Zempsky 2010). The annual incidence rate of pain episodes differs according to SCD phenotype, and ranges between 0.4 and 1.0 episodes per year (Smith 2008). The main locations for acute pain in SCD (in decreasing order of frequency) are upper back, left arm, legs, chest, and lower back (Wilkie 2010).

In most people with SCD, VOCs manifest with general signs and symptoms such as tiredness, dizziness, weakness, yellowing of the eyes, and pallor. More than half have gastrointestinal symptoms (e.g. nausea, vomiting) and respiratory symptoms (e.g. dyspnoea, cough) and about one third have musculoskeletal symptoms (e.g. swelling, tenderness or stiffness in joints) (Jacob 2005).

Description of the intervention

Management of VOCs in people with SCD is mainly symptomatic and uses pharmacologic and non‐pharmacologic compounds to relieve the pain. Pharmacologic management includes non‐opioids, opioids and other miscellaneous agents. Non‐pharmacologic methods such as heat or ice packs, relaxation and acupuncture have no evidence of effectiveness (Ballas 2007). Further management includes optimal hydration by fluid replacement therapy, oxygen administration, treatment of infections, blood transfusion, and physiotherapy (NICE 2012).

Inhaled nitric oxide (iNO) has a critical role in endothelial‐dependent vasodilation and multiple effects on vascular and circulating blood cells. These include the inhibition of platelet aggregation, down‐regulation of cellular adhesion molecules and modulation of ischaemia‐reperfusion injury; these are all pathways adversely affected during VOCs. In addition, iNO is a relatively safe agent that has already been approved by the Food and Drug Administration (FDA) for hypoxic respiratory failure in newborn infants (FDA 1999).

In most studies, iNO is administered via facemask, 80 parts per million (ppm) with 21% final concentration of inspired oxygen, for a duration of four hours (Gladwin 2011; Head 2010; Weiner 2003). Due to the risk of admixture of oxygen with nitric oxide and the subsequent formation of nitrogen dioxide (NO₂), it is important to monitor the nitric oxide and NO₂ concentrations. It is also important to measure methaemoglobin levels regularly, although clinical concentrations of iNO should not cause methaemoglobinaemia. Administration of iNO decreases endogenous nitric oxide production, therefore, rapid withdrawal of iNO can result in a significant rebound pulmonary hypertension, hence iNO should be gradually withdrawn (Creagh‐Brown 2009).

How the intervention might work

One of the factors that may contribute to the physiological disturbances that cause vascular occlusion during pain crises in SCD is the relative, or sometimes absolute, deficiency of nitric oxide (Gladwin 2001). There are a number of effects that nitric oxide has in the human body, most notably in the regulation of vasoconstriction and in the inhibition of platelet aggregation (Gladwin 1999). After diffusing into the smooth muscle cells of the vessels, nitric oxide binds to soluble guanylate cyclase to activate it, which in turn, causes an increase in cyclic guanosine monophosphate (cGMP) (Arnold 1977); this process eventually leads to vascular smooth muscle relaxation (Murad 1985).

Two studies found that levels of nitric oxide metabolites and arginine were low during pain crises in people with SCD and that the severity of the pain was inversely related to nitric oxide levels (Lopez 2000; Morris 2000). One of the mechanisms which explains this is that during pain crises in SCD, there is a high amount of free haemoglobin derived from haemolyzed red blood cells which exceeds the ability of the body to clear it via different mechanisms (such as haptoglobin). The excess free haemoglobin binds to nitric oxide preventing it from playing its role as a vasodilator (Rother 2005).

Why it is important to do this review

Many studies have shown that iNO may have some role in relieving VOCs. However, a systematic review of available evidence is needed to assess the possible benefits and adverse events resulting from the use of iNO.

Objectives

To capture the available body of evidence that evaluates the efficacy and safety of the use of iNO in treating pain crises in people with SCD; and to assess the treatment's relevance, robustness, and validity, in order to better guide medical practice in the fields of haematology and palliative care (since recent literature seems to favour the involvement of palliative care for those people).

Methods

Criteria for considering studies for this review

Types of studies

All blinded randomised controlled trials (RCTs), irrespective of language, will be considered, including parallel, cross‐over and cluster‐randomised trials. We will exclude all quasi‐randomised trials, such as those allocating by using alternate days of the week or surname of the participant.

Types of participants

Our population of interest is people with SCD (SS, SC, Sb+, ad Sb0) proven by electrophoresis, with pain crises. We will include participants of all ages, of both genders, and in any clinical setting (outpatient or inpatient). Trials may include participants with any length of illness who are being treated with iNO for acute pain crises.

Types of interventions

Our intervention of interest is iNO and we will compare it to a placebo (e.g. inhaled nitrogen). We will include any dosage or concentration of iNO and duration of treatment for up to 72 hours of iNO, with follow‐up periods up to the longest reported by the trial.

Types of outcome measures

We will analyse outcomes at end of treatment and for different lengths of follow‐up: up to three months; up to six months; and over six months. We will consider pain as defined by the International Association for the Study of Pain (IASP) "an unpleasant sensory and emotional experience associated with actual or potential tissue damage, or described in terms of such damage" (IASP 2004).

Primary outcomes

1. Resolution of pain crisis by five hours (post hoc change), as defined by

   1. freedom from parenteral opioid use for five hours

   2. pain relief as assessed by visual analogue pain scale score of 6 cm or lower (on 0 to 10 scale)

   3. ability to walk

   4. participant's and family's decision, with physician consensus, that the remaining pain could be managed at home

2. Duration of initial pain crisis until resolution with iNO

3. Frequency of pain crises in the follow‐up period

Secondary outcomes

1. Pain severity measured by

   1. visual analogue score (VAS) for pain (0 to 10 scale)

   2. amount of analgesia used

2. Length of hospital stay (for hospitalised participants)

3. Adverse events in the follow‐up period

   1. clinically important adverse effect – as defined by individual studies

   2. specific adverse events

      1. central nervous system

      2. allergies

      3. blood pressure

      4. haematologic

      5. respiratory

      6. renal

      7. metabolic

      8. other

4. Development of major sickle complications in the follow‐up period (e.g. stroke, acute chest syndrome, pulmonary hypertension, organ damage, blindness, skin ulcers, gallstones, priapism, etc)

5. Death in the follow‐up period (all causes)

Search methods for identification of studies

We searched for trials irrespective of language or publication status (e.g. abstract or online trial report).

Electronic searches

We identified relevant trials from the Cystic Fibrosis and Genetic Disorders Group's Haemoglobinopathies Trials Register using the terms: (sickle cell OR (haemoglobinopathies AND general)) AND nitric oxide.

The Haemoglobinopathies Trials Register is compiled from electronic searches of the Cochrane Central Register of Controlled Trials (CENTRAL) (updated each new issue of The Cochrane Library) and weekly searches of MEDLINE. Unpublished work is identified by searching the abstract books of five major conferences: the European Haematology Association conference; the American Society of Hematology conference; the British Society for Haematology Annual Scientific Meeting; the Caribbean Health Research Council Meetings; and the National Sickle Cell Disease Program Annual Meeting. For full details of all searching activities for the register, please see the relevant section of the Cochrane Cystic Fibrosis and Genetic Disorders Group's website.

Date of most recent search of the Trials Register: 19 September 2019.

We also searched the online trial registries clinicaltrials.gov and the WHO ICTRP (Appendix 1).

Searching other resources

We inspected the reference lists of all included trials for any additional trials. We also contacted the first author of each included trial for any missing information and for information on the existence of any further trials. Finally, we contacted the manufacturers of iNO and ask them for further unpublished relevant trials and for any missing information.

Data collection and analysis

We performed the review following Cochrane recommendations (Higgins 2011a).

Selection of studies

Two authors (TA, OA) independently inspected citations from the searches and identify relevant abstracts. A third author (FA) re‐inspected a random 20% sample of these citations to ensure reliability. Two authors (TA, OA) obtained and inspected full reports of the abstracts meeting the review criteria, in addition to any citations on which the review authors had disagreed. Again, a third author re‐inspected a random 20% of these full reports in order to ensure reliable selection. Where it was not possible to resolve a disagreement by discussion, we attempted to contact the authors of the trial for clarification (Higgins 2011b).

Data extraction and management

1. Data extraction

Two authors (TA, OA) independently extracted data from relevant trials. We discussed any disagreement and documented their decision. If any issues had remained, a third author (FA) would have helped clarify these and documented those final decisions. When the authors were unable to identify the necessary data in the text or tables, we attempted to extract data presented in any graphs and figures; we only included these data if two authors independently extracted the same result.

2. Data management

We used Covidence to screen identified trials and extract the following data:

• trial characteristics (such as trial ID (last name of first author, year of publication): country; clinical setting; objectives; and participant inclusion and exclusion criteria;

• participant characteristics (such as age (mean and standard deviation (SD)), gender, race, sickle cell genotypes, haemoglobin and basic laboratory values, VAS scores);

• details about the intervention(s) and placebos used; and

• outcome data (every outcome listed above) (Covidence 2014).

We also evaluated the risk of bias using the Cochrane risk of bias tool for RCTs (see below).

Assessment of risk of bias in included studies

Working independently, two authors (TA, OA) assessed risk of bias using the tool described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011c). This tool encourages consideration of how the sequence was generated, how allocation was concealed, the integrity of blinding at outcome, the completeness of outcome data, selective reporting and other biases.

The authors assessed the risk of bias in each domain and overall and categorised these as:

• low risk of bias ‐ plausible bias unlikely to seriously alter the results;

• high risk of bias ‐ plausible bias that seriously weakens confidence in the results; or

• unclear risk of bias ‐ plausible bias that raises some doubt about the results.

The authors planned to resolve any disagreements by referring to the trial report, or correspondence with the authors of the report and through discussions and involvement of a third review author (FA). We planned to report any quality assessments where there was lack of agreement between raters.

We summarised the risk of bias for each trial in a summary risk of bias figure.

Measures of treatment effect

1. Dichotomous data

For binary outcomes (adverse events, development of major sickle complications, death), we planned to calculate the risk ratio (RR) and its 95% confidence interval (CI); due to data limitations, we were only able to perform this analysis for the outcomes of the numbers of participants returning to the ED or being re‐hospitalised. It has been shown that RR is more intuitive than odds ratios (Boissel 1999) and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2011). This misinterpretation then leads to an overestimate of the impression of the effect. Where possible, we planned to make efforts to convert outcome measures to dichotomous data. This can be done by identifying cut‐off points on rating scales and dividing participants accordingly into 'clinically improve' or 'not clinically improved'. We planned to assume that if there had been a 50% reduction in a scale‐derived score, this could be considered as a clinically significant response. We planned to test the robustness of this assumption via sensitivity analysis, i.e. by considering other % reductions (see below). If data based on these thresholds were not available, we planned to use the primary cut‐off presented by the original authors.

2. Continuous data

For continuous outcomes (time to resolution of pain, duration of initial pain crisis, frequency of pain crises in the follow‐up period, pain severity and length of hospital stay) we planned to estimate a mean difference (MD) between groups and the related 95% CIs; again due to data limitations we were only able to conduct this type of analysis for pain severity (change in pain score). If different scales had been used, but were of such similarity to allow pooling, we planned to calculate the standardised mean difference (SMD) and, whenever possible, we planned to transform the effect back to the units of one or more of the specific instruments.

Unit of analysis issues

1. Cluster‐randomised trials

Trials increasingly employ 'cluster randomisation' (such as randomisation by clinic or practice), but the analysis and pooling of clustered data poses problems. Firstly, trial authors often fail to account for intra‐class correlation in clustered trials, leading to a 'unit of analysis' error, whereby P values are spuriously low, CIs unduly narrow and statistical significance overestimated (Divine 1992). This causes type I errors (Bland 1997; Gulliford 1999).

To date we have not identified any cluster‐randomised trials, but if we do in future we will employ the following methods. If results from trials are not adjusted for clustering, we will attempt to adjust these results, by multiplying the standard errors (SEs) of the effect estimates (RR or MD, ignoring clustering) by the square root of the design effect. The design effect is calculated as D_Eff = 1 + ((M‐1) ICC), where M is the average cluster size and ICC is the intra‐class correlation co‐efficient (Higgins 2011b). If an ICC is not available from the included trial, the review authors will use other sources to impute ICCs (Campbell 2000).

If a cluster‐randomised trial is appropriately analysed taking into account ICC and relevant data are documented in the report, it is possible to synthesise these trials with parallel group RCTs using the generic inverse variance technique, where the natural logarithm of the effect estimate (and SEs) for all included trials for that outcome is calculated and entered into Review Manager along with the along with the log of the effect estimate (and SEs) from the cluster randomised trial(s).

2. Cross‐over trials

Similarly, we did not identify any cross‐over trials for this review. A major concern of cross‐over trials is the carry‐over effect. It occurs if an effect (e.g. pharmacological, physiological or psychological) of the treatment in the first phase is carried over to the second phase. As a consequence, on entry to the second phase the participants can differ from their initial state despite a washout phase. For the same reason cross‐over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both effects are very likely with pain in people with SCD, if we do identify any cross‐over trials in the future, we will only include the data up to the point of first cross‐over in this review.

Dealing with missing data

We tried to contact the trial authors to access data we considered to be missing from the trial reports, but we have not able to access any additional data.

1. Overall loss of credibility

At some degree of loss of follow‐up data, the results must lose credibility (Xia 2007). The loss to follow‐up in RCTs is often considerable, calling the validity of the results into question. Nevertheless, it is unclear which degree of attrition leads to a high degree of bias. We did not exclude outcomes on the basis of the percentage of participants completing them. However, we used the risk of bias tool described above to indicate potential bias: when more than 25% of the participants left the trials prematurely; when the reasons for attrition differed between the intervention and the control group; and when no appropriate imputation strategies were applied.

2. Dichotomous data

We presented data on a 'once‐randomised‐always‐analysed' basis, assuming an intention‐to‐treat (ITT) analysis.

3. Continuous data

3.1 General

We used an ITT analysis.

3.2 Missing SDs

Where there were missing measures of variance for continuous data but an exact SE and CI are available for group means and either the P value or t value were available for the differences in mean, we calculated the SD value according to the method described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011d). When the SDs are not reported and we could not calculate these from the available data, we asked authors to supply data.

Assessment of heterogeneity

1. Clinical heterogeneity

We initially considered the characteristics of all included trials, before looking at any comparison data, to judge clinical heterogeneity. We inspected all trials for clearly outlying situations.

2. Methodological heterogeneity

Likewise, we considered the characteristics of all included trials, before looking at any comparison data, to judge methodological heterogeneity. We inspected all trials for clearly outlying methods which we had not predicted and discussed them if evident.

3. Statistical heterogeneity

We were not able to present data from multiple trials in a single analysis, but if this is possible in future we assess heterogeneity as follows.

3.1 Visual inspection

We will visually inspect the forest plots which we generate to identify trials with non‐overlapping CIs to suggest the possibility of statistical heterogeneity.

3.2 Employing the I² statistic

We will also investigate heterogeneity between trials by considering the I² statistic alongside the P value for the Chi² test. The I² statistic provides an estimate of the percentage of inconsistency thought to be due to chance (Higgins 2003). The importance of the observed value of I² depends on firstly, the magnitude and direction of effects and secondly, the strength of evidence for heterogeneity (e.g. P value from Chi² test, or a CI for I²).

We will interpret an estimate of I² greater than or equal to 50% accompanied by a statistically significant Chi² statistic as evidence of substantial levels of heterogeneity (Higgins 2003) and we will explore reasons for heterogeneity. If the inconsistency is high and we find clear reasons for this, we will present data separately.

Assessment of reporting biases

We planned to enter data from all identified and selected trials for each outcome into a funnel plot (trial effect versus trial size) in an attempt to investigate the likelihood of overt publication bias, but were not able to do this due to the limited available data. We planned to test for funnel plot asymmetry only for outcomes where we combined 10 or more trials and if the trials were not of similar sizes, as recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Sterne 2011). We planned to use the statistical test by Egger to formally assess funnel plot asymmetry (Egger 1997), and we to supplement this by visual inspection of the forest plot to differentiate small trial effects from other reasons for funnel plot asymmetry.

Data synthesis

We understand that there is no definitive argument for the preference of fixed‐effect or random‐effects models. The random‐effects method incorporates an assumption that the different trials are estimating different, yet related, intervention effects. This often seems to be true to us and the random‐effects model takes into account differences between trials, even if there is no statistically significant heterogeneity. There is, however, a disadvantage to the random‐effects model; it adds weight to small trials, which often are the most biased ones (Sterne 2011). Depending on the direction of effect, these trials can either inflate or deflate the effect size. Therefore, we have used the fixed‐effect model for all analyses. The reader is, however, able to choose to inspect the data using the random‐effects model in the published review.

Subgroup analysis and investigation of heterogeneity

1. Subgroup analyses

If we had been able to identify substantial heterogeneity (as defined above), we would have attempted to present data for people with SCD in similar states and stages together. For primary outcomes, we would also have reported subgroup analyses of different stages of pain crisis (prodromal, initial, established, and resolving) if the data had existed. We also intended to undertake subgroup analyses comparing participants who had experienced serious adverse events of SCD (e.g. renal and haemodynamic adverse effects) at baseline to those who did not; in addition we planned to compare participants who had severe pain at baseline compared to those who did not have severe pain at baseline.

We planned to analyse data from published trials (those with a report in peer‐reviewed journals) and compare these findings with outcomes from trials that have not yet appeared in full report in peer‐reviewed journals. We proposed commenting on these findings, but not take action on them. All trials included in this review have been published in peer‐reviewed journals.

We also planned to analyse the primary outcomes from trials funded or supported by industry and compare these data with those from more independent trials. Again, we proposed to comment on these findings but not exclude or include trials because of them. Due to data limitations we were not able to do this.

2. Investigation of heterogeneity

As we were mostly only able to present data from a single trial for each outcome, we did not investigate heterogeneity. If we are able to combine data from multiple trials in the future and if inconsistency is high, we will report this. Firstly, we will investigate whether data have been entered correctly. Secondly, if data are correct, we will visually inspect the graph and successively remove trials from the analysis to see if homogeneity is restored. If this should occur with no more than 10% of the data being excluded, we will present the data; if not, we will not pool the data and will discuss the issues.

If unanticipated clinical or methodological heterogeneity is obvious, we will simply state hypotheses regarding these for future reviews or versions of this review. We do not anticipate undertaking analyses relating to these.

Sensitivity analysis

Due to data limitations, we were not able to undertake any of our planned sensitivity analyses in this version of the review. In future these analyses will only apply to the primary outcomes. We are conscious of the risk of finding significant results due to the play of chance secondary to multiple analyses and if we become concerned about multiple testing yielding chance findings, we will use 99% rather than 95% CIs.

1. Risk of bias

We will analyse the effects of excluding trials that we judged to be at a high risk of bias across one or more of the following domains for the meta‐analysis of the primary outcome: randomisation (implied as randomised with no further details available); allocation concealment; blinding; and outcome reporting. If the exclusion of trials at a high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then we will include data from these trials in the analysis.

2. Imputed values

We will also undertake a sensitivity analysis to assess the effects of including data from trials where we imputed values. If we note substantial differences in the direction or precision of effect estimates, we will not pool data but instead present them separately.

3. Fixed‐effect analysis and random‐effects analysis

We will synthesise data for the primary outcome using a random‐effects model to evaluate whether the greater weights assigned to smaller trials altered the significance of the results, compared with the less evenly distributed weights in the fixed‐effect model.

4. Clinical response

We will assume that if there had been a 50% reduction in a scale‐derived score, this could be considered as a clinically significant response. We will, however, test the robustness of this assumption via sensitivity analysis, i.e. by considering other percentages reductions such as 25% and 75%.

Summary of findings table

Two review authors (TA, OA) assessed the quality of the evidence for each outcome across the included trials using the GRADE guidelines (Guyatt 2011). In case of discrepancy, a third author assessed the quality and resolved any issues by discussion. We presented our findings for the following outcomes in a 'Summary of findings' table using GRADEpro.

1. Time to resolution of initial pain crisis

2. Frequency of pain crises in the follow‐up period (return to ED within 30 days)

3. Frequency of pain crises in the follow‐up period (re‐hospitalisation within 30 days)

4. Adverse events (end of trial)

In a post hoc change we have reported the frequency of pain crises in terms of both the return to the ED and re‐hospitalisation.

Results

Description of studies

Results of the search

We identified 10 references to seven trials in the literature search. Four of these trials were considered eligible after the initial screening. Further full‐text screening excluded one further trial and only three trials were included in this review.

The PRISMA flow diagram details the search, assessment for eligibility and inclusion of trials (Figure 1).

1.

Study flow diagram.

Included studies

All three included trials were published in English in peer‐reviewed journals (Gladwin 2011; Head 2010; Weiner 2003). For more detailed information, see Characteristics of included studies.

Study design

All included trials were conducted in the USA and all were of parallel design (Gladwin 2011; Head 2010; Weiner 2003). The trials were conducted over a period varying between two years (Weiner 2003) and four years (Gladwin 2011). The largest trial was multicentre and conducted at the EDs of 11 centres (Gladwin 2011). The remaining two trials were conducted in single hospitals (Head 2010; Weiner 2003). In all the three trials, participants were randomised into the intervention or control group and they were described as being blinded.

Participants

The largest trial recruited 150 participants (Gladwin 2011), the remaining two trials recruited 18 participants (Head 2010) and 20 participants (Weiner 2003). Most participants were young adults, with a median age of 24.2 years (Gladwin 2011) and mean age of 32.1 years (Head 2010); however, one trial was conducted in a paediatric hospital where most participants were children with a mean age of 17.6 years (Weiner 2003). The number of males and females was equal in all the trials. Almost all of the participants had HbSS genotype in two of the trials; 100% in one study (Head 2010) and 90% in a second (Gladwin 2011). However, the third trial had a variety of genotypes with 50% of participants having HbSS genotype (Weiner 2003). The majority of participants (59%) were using hydroxyurea in the largest trial (Gladwin 2011), while hardly any participants were using the drug in the remaining trials; none in one trial (Head 2010) and just one participant in the final trial (Weiner 2003).

Interventions

The intervention in the large trial was iNO balanced with nitrogen (99.92% grade 5 nitrogen, 0.08% pharmaceutical grade nitric oxide) for a total duration of eight hours, and a dose of 80 ppm in the first four hours then 40 ppm for a further four hours; the control group received a placebo of 100% grade 5 nitrogen (Gladwin 2011). Both iNO and placebo were delivered with air and mixed with oxygen to achieve a constant fraction of inspired oxygen (FiO₂) of 24%. In the remaining two studies the intervention was iNO 80 ppm for four hours, and the control was room air (Head 2010; Weiner 2003).

Outcome measures

The primary outcome in two trials was the change in pain score after four hours of inhalation as measured by a 10 cm VAS (Head 2010; Weiner 2003). Whereas in the larger trial, the primary outcomes were the time for pain resolution as defined by freedom from parenteral opioid use for five hours, VAS score of 6 cm or lower, and the ability to walk (Gladwin 2011). The secondary outcome measures in all the three trials include the amount of opioids used over different periods of time. Two trials reported the length of hospitalisation (Gladwin 2011; Weiner 2003) and one of these also evaluated the number of discharges in the first 24 hours, returns to ED within 30 days, and the rate of acute chest syndrome or pneumonia requiring blood transfusion (Gladwin 2011). On the other hand, the third trial did not report on the duration of hospitalisation, and instead reported on the time spent in the ED (Head 2010).

Excluded studies

On first evaluation of the search results, we excluded studies that did not report on the intervention of interest (iNO) or did not report on the population of interest (people with SCD experiencing a pain crisis). We also excluded narrative reviews, case reports and case series. We further considered the four trials listed as excluded and described the reasons for the exclusion of these trials in the tables (Characteristics of excluded studies).

One was a trial of nitric oxide bioavailability in people with SCD who were not experiencing pain crises (Gladwin 2003). The second was a trial of iNO, prostacyclin and oxygen in people with SCD and pulmonary hypertension, not pain crises (Jison 2004). A further trial assessed iNO in people with SCD and acute chest syndrome, not pain crises (Maitre 2014). The fourth trial was about treatemnt of leg ulcers in sickle cell disease with no relation to sickle cell crises (Steinberg 2014).

Risk of bias in included studies

The included body of literature in this systematic review is of moderate risk of bias (Figure 2). The included trials were mostly showing unclear to low risk of bias across all assessment domains except for one trial which was partially supported by a for‐profit entity (Head 2010). More specifically the largest trial had an overall low risk of bias (Gladwin 2011), while one had an overall high risk of bias (Head 2010) and the third had a moderate risk of bias overall (Weiner 2003).

2.

Risk of bias summary: review authors' judgements about each risk of bias item for each included study.

Allocation

Sequence generation

Two trials did not describe the method of generating the randomisation sequence and were judged to have an unclear risk of bias (Head 2010; Weiner 2003). The third study described using block randomisation but did not clarify exactly how the sequence was generated, so was also judged to have an unclear risk of bias (Gladwin 2011).

Allocation concealment

Two of the three included trials did not described how the randomisation sequence was concealed and were judged to have an unclear risk of bias (Head 2010; Weiner 2003). The third study described how randomisation was defined at the time a set of placebo or nitric oxide gas cylinders was assigned and a cylinder was opened. The cylinders displayed coded labels which were applied at the manufacturing site. Therefore, this study was judged to have a low risk of bias for allocation concealment (Gladwin 2011).

Blinding

One trial reported that all the participants and investigators remained blinded to group assignment, all cylinders and gas delivery systems were identical in both groups, and that the investigators were blinded to the type of intervention used (Gladwin 2011). In addition, the data set was analysed by the steering committee, independently of the sponsor, using prespecified analyses, end points, and subgroups. Therefore this trial was determined to have a low risk for bias for blinding. The other two trials were also described as double‐blinded, but with fewer details than the previously mentioned trial. The paediatric trial stated that the the investigators, participants, and parents of participants remained blinded throughout the trial, which therefore had a low risk of bias (Weiner 2003). Conversely, the third trial stated that the attending physician was blinded to the type of intervention used but failed to mention whether the personnel who collected that data were blinded or not (Head 2010). We therefore judged this trial to have an unclear risk of bias.

Incomplete outcome data

There was no reported loss of follow‐up in one trial (Head 2010). The paediatric trial stated that after randomisation but before initiation of inhalation, five participants did not meet final eligibility criteria; however, all 20 participants who began inhalation completed the trial (Weiner 2003). The largest trial reported that eight participants (four from each group) out of a total of 150 participants discontinued treatment due to various reasons, although they were included in the ITT analysis (Gladwin 2011).

Therefore we concluded a low risk of attrition bias for all the trials.

Selective reporting

We were able to retrieve the published protocol for the most recent trial and all the primary and secondary outcomes reported in this trial are identical to the registered protocol (Gladwin 2011). We judged this trial to have a low risk of selective reporting bias.

We could not find the registered protocols for either of the remaining two trials (Head 2010; Weiner 2003). We therefore compared the outcomes listed in the 'Methods' section in the final publication to those presented in the 'Results' section and the outcomes were identical. Therefore we judged the risk of selective reporting bias for these two studies to be unclear (Head 2010; Weiner 2003).

Other potential sources of bias

There was a financial conflict of interest due to support from a corporate entity in one trial (Head 2010). In addition, two trials had too small a sample size to potentially detect a meaningful difference between treatment groups (Head 2010; Weiner 2003).

Effects of interventions

See: Table 1

Primary outcomes

1. Resolution of pain crises in five hours

None of the trials reported this outcome (Gladwin 2011; Head 2010; Weiner 2003).

2. Duration of initial pain crisis until resolution with iNO

One trial (n = 150) reported that the median time to resolution of a pain crisis was 73.0 hours (95% CI 46.0 to 91.0) in the iNO group and 65.5 hours (95% CI 48.1 to 84.0) in the placebo group (Gladwin 2011) (low‐quality evidence).

The two smaller trials did not evaluate this outcome (Head 2010; Weiner 2003).

3. Frequency of pain crises in the follow‐up period

The largest trial (n = 150) reported 10.8% (8 out of 75) participants in the treatment group and 15.1% (11 out of 75) participants in the control group returned to the ED within 30 days, RR 0.73 (95% CI 0.31 to 1.71) (Analysis 1.1) (low‐quality evidence). Further, in the iNO group 12.2% (9 out of 75) participants and in the control group 23.0% (17 out of 75) participants were re‐hospitalised, RR 0.53 (95% CI 0.25 to 1.11) (Analysis 1.2) (low‐quality evidence). Neither of these results was statistically significant (Gladwin 2011).

1.1. Analysis.

Comparison 1 Inhaled nitric oxide versus placebo, Outcome 1 Participants returning to emergency department.

1.2. Analysis.

Comparison 1 Inhaled nitric oxide versus placebo, Outcome 2 Participants rehospitalised.

The two smaller trials did not report this outcome (Head 2010; Weiner 2003).

Secondary outcomes

1. Pain severity

a. visual analogue pain scale score (0 to 10 scale)

The largest trial (n = 150) reported this outcome at two, four, six and eight hours (Gladwin 2011), one trial reported at three, four and six hours (Weiner 2003) and the remaining trial only reported this outcome at four hours (Head 2010). Only two trials provided data for the analysis (Gladwin 2011; Head 2010).

At two hours, Gladwin reported the difference between groups in mean change of VAS score, MD 0.30 cm (95% CI ‐0.19 to 0.79) (Analysis 1.3).

1.3. Analysis.

Comparison 1 Inhaled nitric oxide versus placebo, Outcome 3 Change in VAS pain score.

At three hours, one trial (n = 20) reported that the difference in decrease in VAS pain score between groups was approaching statistical significance with P = 0.05, but there were no data available for analysis (Weiner 2003).

At four hours, the largest trial reported no difference in the decrease in VAS score between groups, MD 0.20 cm (95% CI ‐0.50 to 0.90) (Gladwin 2011). At the same time‐point, a second trial reported a significant difference in pain reduction favouring iNO measured by VAS, MD ‐3.33 cm (95% CI ‐5.32 to ‐1.34) (Head 2010). However, when these data were combined there was no significant difference between iNO and placebo for reducing pain at four hours, MD ‐0.19 cm (95% CI ‐0.84 to 0.47) (Analysis 1.3). The third trial reported a mean change of ‐ 2.0 cm for the iNO group and ‐1.2 cm in the placebo group four hours after the intervention and the P value of the difference between the two groups was 0.37 (Weiner 2003).

At six hours Gladwin reported no difference between groups for the change of VAS score, MD ‐0.10 cm (95% CI ‐0.80 to 0.60) (Analysis 1.3).

Finally, at eight hours, Gladwin reported the difference in the change of VAS score, which again was not statistically significant, MD ‐0.10 cm (95% CI ‐0.80 to 0.60) (Analysis 1.3).

b. amount of analgesia used

All three trials reported on this outcome, but none provided data that could be analysed (Gladwin 2011; Head 2010; Weiner 2003).

Gladwin reported the median (interquartile range (IQR)) amount of opioid used at four and eight hours after the intervention and also the total amount (Gladwin 2011). At four hours after the intervention, Gladwin reported a median (IQR) of 0.33 mg/kg (0.2 to 0.7) was required in the iNO group and 0.33 mg/kg (0.1 to 0.6) in the placebo group. At eight hours the median amount of opoid used had dropped to 0.28 mg/kg (0.09 to 0.54) for the iNO group and 0.23 mg/kg (0.07 to 0.70) for the placebo group. The total amount of opioid used for the iNO group was 2.8 mg/kg (1.4 to 6.1) and for the placebo group 2.9 mg/kg (1.1 to 9.9) (Gladwin 2011).

Head did not report any numeric data for this outcome, but stated that the total amount of morphine used by the iNO group was slightly less than the control group; however, the difference was both statistically and clinically insignificant (P = 0.26) (Head 2010).

Weiner reported the mean amount of opoid at four hours, six hours and a total over 24 hours (Weiner 2003). At four hours after the intervention, the mean amount of opioid used in the iNO group was 0.26 mg/kg and in the placebo group 0.32 mg/kg (Weiner 2003). However, at six hours this had increased to 0.29 mg/kg for the iNO group and 0.44 mg/kg for the placebo group. Over 24 hours, the mean amount of opioid used was 0.63 mg/kg for the iNO group and 0.91 mg/kg for the placebo group.

2. Length of hospital stay (for hospitalised participants)

Two trials reported this outcome, both stating the median duration of hospitalisation (Gladwin 2011; Weiner 2003). Gladwin reported the median (IQR) number of days spent in the hospital was 4.1 days (2.0 to 6.0) for the iNO group and 3.1 days (1.7 to 6.4) for the placebo group (Gladwin 2011). Weiner reported the median duration of hospitalisation was 78 hours for the treatment group and 100 hours for the controls, but did not report any ranges (Weiner 2003).

3. Adverse events

Only the larger trial reported the number of serious adverse events in the iNO group during or after the intervention compared to the control group (Gladwin 2011). The paper reported that acute chest syndrome developed in five out of 75 participants (6.7%) from each group (95% CI 2.2 to 14.9), which showed no difference between iNO and control, RR 1.00 (95% CI 0.30 to 3.31). The paper also reported that pyrexia was recorded in one participant (1.3%) from each group (95% CI 0.03 to 7.2), again showing no difference between groups, RR 1.00 (95% CI 0.06 to 15.69). Dysphagia, the sensation of a foreign body and a drop in haemoglobin were each reported in one participant (1.3%) in the iNO group (95% CI 0.03 to 7.2) but not in the placebo group, RR 3.00 (95% CI 0.12 to 72.49) (all low‐quality evidence) (Analysis 1.4). The two smaller trials did not report on the adverse events (Head 2010; Weiner 2003).

1.4. Analysis.

Comparison 1 Inhaled nitric oxide versus placebo, Outcome 4 Adverse events.

Discussion

We carried out this systematic review of the literature and were only able to include three trials of interest (Gladwin 2011; Head 2010; Weiner 2003). While we were able to analyse some limited data, there were not enough quantitative data to conduct a meta‐analysis. Therefore, we reported most of the outcomes narratively.

Summary of main results

The currently available body of evidence from the three trials (n = 188) currently eligible for inclusion in this review is heterogenous, particularly in outcome measurements. Only one addressed the outcomes of "time to pain to pain resolution" and "frequency of pain crises in the follow‐up period" (Gladwin 2011). The trial reported that the median time to pain resolution was shorter in the iNO group compared to placebo and results were not statistically significant difference in terms of recurring pain crises and rehospitalization between the two groups (Analysis 1.1; Analysis 1.2).

It is not clear whether iNO reduces the pain on a VAS score. Two trials reported a beneficial effect of nitric oxide in acute vaso‐occlusive crises in terms of reducing VAS score after four hours of the intervention (Head 2010; Weiner 2003), but only one of them reported data (Head 2010). These trials, however, were small and showed more limitations, compared to the third trial which was multicentre and included significantly more participants and continued for a longer period of time (Gladwin 2011). Data from this trial did not show any significant benefit when analysed at any time point up to eight hours (Analysis 1.3).

It is also not clear if iNO has any benefit in reducing the amount of analgesia used or in shortening the hospital stay for individuals with acute sickle cell pain crises. Narcotic use between the two groups of participants was approximately the same in one trial (Gladwin 2011), and while slightly different in the remaining trials the difference was not statistically significant (Head 2010; Weiner 2003). This suggests that this difference could possibly be due to chance, taking the sample size of the trials into consideration.

Overall completeness and applicability of evidence

The available body of evidence that addresses the question of this review is quite small and insufficiently homogenous to produce a conclusive result. The included trials did, however, set out and attempt to answer the review question quite directly, although using different methods of outcome measurement and reporting. These trials included the same type of participants and evaluated the same type of intervention and comparison of interest. The heterogeneity that exists in this body of evidence does not threaten the external validity of the results, but hinders the attempts of producing a conclusive clinical recommendation.

Two trials reported the data using medians and IQRs which prevented us from conducting an analysis in Review Manager software (Gladwin 2011; Weiner 2003); furthermore, one of them was missing some essential data needed to conduct the meta‐analysis (Weiner 2003). Also, the third study only used diagrams to report the data without clearly stating the numbers in the published full text and, unfortunately, we were not able to extract the data accurately from the diagrams. In addition there was some conflict between the reported data and the diagrams in the trial report (Head 2010). We attempted to contact the authors to obtain the necessary data but either we were unable to reach them (Head 2010) or the authors were not able to share the data with us (Weiner 2003).

In this topic area, there is lack of well‐conducted RCTs with long‐term follow‐up and with a sufficiently large sample size. The currently available data are insufficient to offer a conclusive answer on the effectiveness of iNO use for individuals with SCD experiencing acute pain crises. We also noted discrepancy in the identified trials within this review, particularly with regard to which clinical outcomes they reported. A systematic review and meta‐analysis may help resolve the question in cases of inconclusive or conflicting trials; however, this requires the trials to be sufficiently homogenous, particularly in their outcome measurements.

Quality of the evidence

Overall, using the GRADE assessment we judged the evidence to be of low quality. This downgrade in quality was mainly due to an unclear risk of selection bias (a lack of description of exactly how the randomisation sequence was generated and concealed) and also low precision (small numbers of events and wide CIs).

Potential biases in the review process

This review was conducted by three researchers who have independently undertaken screening and data extraction from the three included trials. This was planned a priori to reduce any selection bias or errors in data retrieval. The initial search was performed by an experienced librarian to ensure a comprehensive coverage of the available literature on this topic.

Agreements and disagreements with other studies or reviews

No other systematic reviews or non‐randomised studies were identified in the literature to which we could compare our findings.

Authors' conclusions

Implications for practice.

Currently, and based on the included trials, there is no enough evidence to support the use of inhaled nitric oxide in treating pain crises in people with sickle cell disease.

Implications for research.

Further large‐scale, well‐conducted and long‐term trials are needed to provide more robust data on the effects of inhaled nitric oxide on vaso‐occlusive crises in people with sickle cell disease. Such trials need to offer patient‐important outcomes that are measured and reported in a standardized form. Such outcomes would include consistent effect measures of pain and time to pain resolution and amounts of analgesics used. The outcomes of healthcare services use would also need to be measured and reported consistently across the trials.

Appendices

Appendix 1. Electronic search strategies

Database	Date searched	Search strategy
Clinicaltrials.gov (clinicaltrials.gov)	26/09/2019	search terms used: Inhaled NO AND sickle cell, Inhaled nitric oxide AND sickle cell, INO AND sickle cell, sickle cell crises, Vaso‐occlusive Crisis.
WHO ICTRP (apps.who.int/trialsearch/)	17/03/2018	search terms used: Inhaled NO AND sickle cell, Inhaled nitric oxide AND sickle cell, INO AND sickle cell, sickle cell crises, Vaso‐occlusive Crisis.

Data and analyses

Comparison 1. Inhaled nitric oxide versus placebo.

Outcome or subgroup title	No. of studies	No. of participants	Statistical method	Effect size
1 Participants returning to emergency department	1		Risk Ratio (M‐H, Fixed, 95% CI)	Subtotals only
1.1 At up to 30 days	1	150	Risk Ratio (M‐H, Fixed, 95% CI)	0.73 [0.31, 1.71]
2 Participants rehospitalised	1		Risk Ratio (M‐H, Fixed, 95% CI)	Subtotals only
2.1 At 30 days	1	150	Risk Ratio (M‐H, Fixed, 95% CI)	0.53 [0.25, 1.11]
3 Change in VAS pain score	2		Mean Difference (IV, Fixed, 95% CI)	Subtotals only
3.1 At 2 hours	1	150	Mean Difference (IV, Fixed, 95% CI)	0.30 [‐0.19, 0.79]
3.2 At 4 hours	2	168	Mean Difference (IV, Fixed, 95% CI)	‐0.19 [‐0.84, 0.47]
3.3 At 6 hours	1	150	Mean Difference (IV, Fixed, 95% CI)	‐0.10 [‐0.80, 0.60]
3.4 At 8 hours	1	150	Mean Difference (IV, Fixed, 95% CI)	‐0.10 [‐0.80, 0.60]
4 Adverse events	2		Risk Ratio (M‐H, Fixed, 95% CI)	Subtotals only
4.1 Acute chest syndrome	1	150	Risk Ratio (M‐H, Fixed, 95% CI)	1.0 [0.30, 3.31]
4.2 Pyrexia	1	150	Risk Ratio (M‐H, Fixed, 95% CI)	1.0 [0.06, 15.69]
4.3 Dysphagia	1	150	Risk Ratio (M‐H, Fixed, 95% CI)	3.0 [0.12, 72.49]
4.4 Drop in haemoglobin	1	150	Risk Ratio (M‐H, Fixed, 95% CI)	3.0 [0.12, 72.49]

Characteristics of studies

Characteristics of included studies [ordered by study ID]

Gladwin 2011.

Methods	Trial design: prospective, double‐blind, placebo‐controlled RCT. Location: 11 centres in USA. Duration: single treatment with each lasting 8 hours; trial conducted between 05 October 2004 and 22 December 2008.
Participants	Participants with VOCs of SCD enrolled and randomised. 75 participants in each group, balanced in terms of age, sex, genotype, hydroxyurea use, vitals signs, pain scores, and laboratory values. Age (median (IQR)): overall 24.2 (17.4 ‐ 33.7) years, iNO group 22.9 (17.8 ‐ 33.9) years, placebo group 24.5 (17.1 ‐ 31.8) years. Gender split (n (%)): overall 75 (50%) males, iNO group 37 (49.3%) males, placebo group 38 (50.7%) males. Sickle cell genotypes (%): HbSS: overall 90.7%, iNO group 93.3%, placebo group 6.7%; HbS‐βthal: overall 9.3%, iNO group 88.0%, placebo group 12.0%. Hydroxyurea use (%): overall 59.3%, iNO group 57.3%, placebo group 61.3%.
Interventions	Treatment: iNO 80 ppm balanced with nitrogen (99.92% grade 5 nitrogen, 0.08% pharmaceutical grade NO2) for 4 hours, followed by 40 ppm for 4 hours. Control: 100% grade 5 nitrogen for 8 hours. Both balanced with 24% final concentration of inspired oxygen. For participants remaining in the hospital after the initial 8‐hour dose, the gas was administered through a pulsed‐flow delivery system with 1 L continuous oxygen via nasal cannula at a dose of 6 mL/pulse/breath of 800 ppm NO2 for a body weight of 27 kg or greater, or 3 mL/pulse/breath if less than 27 kg, up to a maximum of 72 hours total gas administration.
Outcomes	Primary outcome measure: time to resolution of painful crisis, defined by (1) freedom from parenteral opioid use for 5 hours; (2) pain relief as assessed by VAS scores of 6 cm or lower (on 0 ‐ 10 scale); (3) ability to walk; and (4) participant's and family's decision, with physician consensus, that the remaining pain could be managed at home. Secondary outcome measures: length of hospitalisation (from admission to discharge), VAS score over time, total dose of opioids in the first 8 hours after enrolment and during the entire hospitalisation, rate of ACS or pneumonia requiring blood transfusion, proportion discharged in the first 24 hours, proportion returning to hospital within 30 days, and change in nitrate/nitrite levels and methemoglobin levels as measures of NO2 metabolism and reactions in the blood, pain relapse (proportion of participants treated again for pain within 24 hours and within 30 days after hospital discharge) and adverse events.
Notes	clinicaltrials.gov Identifier: NCT00094887.
Risk of bias
Bias	Authors' judgement	Support for judgement
Random sequence generation (selection bias)	Unclear risk	Participants randomised using block randomisation by site and age at entry (10 ‐ 15 years and > 15 years), in blocks of 4, in a 1:1 ratio. but no mention of how the list was generated.
Allocation concealment (selection bias)	Low risk	Randomisation was defined at the time a set of trial placebo or NO2 gas cylinders was assigned and a cylinder was opened. Coded labels were applied to the cylinders at the manufacturing site.
Blinding of participants and personnel (performance bias) All outcomes	Low risk	Participants and investigators remained blind to group assignment, cylinders were coded and a “blinded” version of the face mask NO2 delivery system blanked out and covered the NO2 and nitrogen dioxide monitor displays. The placebo gas was administered in the same way and over the same time to ensure that participants and investigators remained blind to group assignment.
Blinding of outcome assessment (detection bias) All outcomes	Low risk	The investigators were blinded to the type of intervention used: the data set was analysed by the steering committee, independently of the sponsor, using prespecified analyses, end points, and subgroups.
Incomplete outcome data (attrition bias) All outcomes	Low risk	Although 8 participants (4 from each group) out of 150 discontinued treatment due to various reasons, they were included in the ITT analysis.
Selective reporting (reporting bias)	Low risk	The primary and secondary outcomes presented in the trial report are identical to those in the registered protocol.
Other bias	Low risk	Sample size was estimated based on data from a previous study of NO2 therapy in children and the Agency for Healthcare Research and Quality predicting a mean length of stay approximating 106 hours. At the end of the trial, the data set was analysed by the steering committee, independently of the sponsor, using prespecified analyses, end points, and subgroups.

Head 2010.

Methods	Trial design: prospective, double‐blind, placebo‐controlled RCT. Location: USA. Duration: single treatment with each lasting 4 hours.
Participants	Adults experiencing acute VOCs. 9 participants in each group. Age (mean (SD)): iNO group 32.1 (9.8) years, placebo group 28.75 (5.578) years. Gender split (n): iNO group 6 males, placebo group 5 males. Sickle cell genotypes (n): all participants have HbSS genotype. Hydroxyurea use (n): iNO group 0, placebo group 0.
Interventions	Treatment: iNO (80 ppm with 21% final concentration of inspired oxygen) for 4 hours. Control: 21% inspired oxygen for 4 hours. Participants meeting eligibility criteria received standard ED treatment with pain medication consisting of intravenous morphine sulphate (initial dose up to 0.3 mg/kg body weight) and fluids (isotonic sodium chloride solution, 10 mL/kg over 30 min). Additional intravenous morphine was delivered on demand by a PCA device (1 ‐ 4 mg per dose with a lockout period). The gas was given within 60 min after the initial intravenous morphine injection.
Outcomes	Primary outcome: reduction in pain scores at 4 hours of inhalation, measured on a 10 cm VAS. Secondary outcome: amount of PCA‐administered narcotic used at baseline, 4 hours, and 6 hours. Safety assessments included systolic blood pressure, pulse oximetry, concentration of delivered NO2, and concentration of methaemoglobin.
Notes
Risk of bias
Bias	Authors' judgement	Support for judgement
Random sequence generation (selection bias)	Unclear risk	The trial states that participants were randomised into 2 groups after their initial evaluation, but no clear description for the exact method of randomisation was reported.
Allocation concealment (selection bias)	Unclear risk	There was no mention of how allocation was concealed or not.
Blinding of participants and personnel (performance bias) All outcomes	Low risk	There was no mention of whether or not the participants or all the personnel were blinded. However, the trial stated that it was a double‐blind and that the attending physician was blinded to the type of intervention used. Therefore, we concluded that the participants were blinded.
Blinding of outcome assessment (detection bias) All outcomes	Unclear risk	There is no mention whether the personnel who collected that data were blinded or not.
Incomplete outcome data (attrition bias) All outcomes	Low risk	There was no loss to follow‐up or withdrawal reported in the trial.
Selective reporting (reporting bias)	Unclear risk	The protocol for this RCT was not retrievable on search efforts to compare to and find out if some outcomes were not reported, but the all the outcomes reported in the Methods section in the final publication were reported in the Results section.
Other bias	High risk	Financial conflict of interest exists, as the trial was supported by for‐profit industry. The lead authors also hold patents of technologies evaluated in this trial. Sample size is potentially too small to detect a meaningful difference.

Weiner 2003.

Methods	Trial design: prospective, double‐blind, placebo‐controlled RCT. Location: urban tertiary care academic children's hospital in USA. Duration: single treatment with each lasting 4 hours, trial conducted between September 1999 and October 2001.
Participants	Participants aged 10 to 21 years with SCD and severe acute vaso‐occlusive crisis. 10 participants in each group. All were African Americans. Age (mean (SD)): iNO group 17.6 (2.48) years, placebo group 15.2 (2.6) years. Gender split (n): iNO group 6 males, placebo group 5 males. Sickle cell genotypes (n): HbSS: iNO group 4, placebo group 6; HbSC: iNO group 5, placebo group 4; HbS‐βthal: iNO group 1, placebo group 0 Hydroxyurea use (n): iNO group 1, placebo group 0.
Interventions	Treatment: iNO (80 ppm with 21% final concentration of inspired oxygen) for 4 hours. Control: 21% inspired oxygen for 4 hours. Participants meeting eligibility criteria received standard ED treatment with morphine (0.1 mg/kg to a maximum of 6 mg) and fluids (isotonic sodium chloride solution, 10 mL/kg over 30 minutes). Additional morphine was delivered by PCA pump (0.025 mg/kg per dose with a 7‐minute lockout and a 0.3‐mg/kg 4 hour cumulative dose lockout). The gas was given within 90 min of the initial ED morphine dose.
Outcomes	Primary outcome: change in pain score at 4 hours of inhalation, measured on a 10 cm VAS. Secondary outcomes: amount of parenteral narcotic used 4, 6, and 24 hours after initiating inhalation, and length of hospitalisation. Safety assessments included minimum systolic blood pressure, minimum SpO2, maximum concentration of delivered NO2, and maximum concentration of methaemoglobin.
Notes
Risk of bias
Bias	Authors' judgement	Support for judgement
Random sequence generation (selection bias)	Unclear risk	The trial mentions that the participants were randomised into the 2 groups. Although no clear description for the exact method of randomisation was reported.
Allocation concealment (selection bias)	Unclear risk	There was no mention of how allocation was concealed or not.
Blinding of participants and personnel (performance bias) All outcomes	Low risk	Described as double‐blind. In addition the authors mentioned that the the investigators, participants, and parents of participants had remained blinded throughout the trial.
Blinding of outcome assessment (detection bias) All outcomes	Low risk	Authors mentioned that the the investigators, participants, and parents of participants had remained blinded throughout the trial.
Incomplete outcome data (attrition bias) All outcomes	Low risk	No loss of follow‐up was reported. 25 participants were randomised; after randomisation but before initiation of inhalation, 5 participants did not meet final eligibility criteria. All 20 participants who began inhalation, completed the trial.
Selective reporting (reporting bias)	Unclear risk	The protocol for this RCT was not retrievable on search efforts to compare to and find out if some outcomes were not reported, but the all the outcomes reported in the Methods section in the final publication were reported in the Results section.
Other bias	High risk	Sample size is potentially too small to detect a meaningful difference.

ACS: acute chest syndrome
 ED: ED
 iNO: inhaled nitric oxide
 IQR: interquartile range
 ITT: intention‐to‐treat
 NO₂: nitric oxide
 PCA: patient‐controlled analgesia
 ppm: parts per million
 RCT: randomised controlled trial
 SCD: sickle cell disease
 SD: standard deviation
 SpO₂: blood oxygen saturation
 VAS: visual analogue scale
 VOC: vaso‐occlusive crises

Characteristics of excluded studies [ordered by study ID]

Study	Reason for exclusion
Gladwin 2003	Trial of NO bioavailability in people with SCD, by measuring forearm blood flow after intra‐arterial infusions of acetylcholine, nitroprusside, and L‐NMMA (NO synthase inhibitor). The participants, interventions, and outcomes did not meet the inclusion criteria.
Jison 2004	Trial of iNO, prostacyclin and oxygen in people with SCD and pulmonary hypertension, not pain crises. The participants, interventions, and outcomes did not meet the inclusion criteria.
Maitre 2014	Trial of iNO in people with SCD and acute chest syndrome, not pain crises. The participants and outcomes did not meet the inclusion criteria.
Steinberg 2014	Trial is looking into treamtent of leg ulcers in sickle cell disease, not pain crises. The participants, interventions, and outcomes did not meet the inclusion criteria.

iNO: inhaled nitric oxide
 NO: nitric oxide
 SCD: sickle cell disease

Differences between protocol and review

At draft protocol stage we included the primary outcome 'Resolution of pain crisis by five hours', but removed it from the final version following peer review comments. However, at full review stage we decided to re‐instate this primary outcome.

Contributions of authors

Protocol stage: all the authors have contributed to the drafting of the Background section of the protocol; FA supervised and reviewed all the drafts, and has drafted the Methods section. All the authors have contributed to the design of the review and its coordination, and have all approved the final form of the protocol draft.

Review stage: all authors have contributed to the final review version. TA and OA extracted data, assessed risk of bias and produced the GRADE assessments. FA adjudicated on any disagreements. TA and OA drafted text and FA commented on text.

Sources of support

Internal sources

• No sources of support supplied

External sources

• National Institute for Health Research, UK.

  This systematic review was supported by the National Institute for Health Research, via Cochrane Infrastructure funding to the Cochrane Cystic Fibrosis and Genetic Disorders Group.

Declarations of interest

Tarek Aboursheid declares no potential conflicts of interest (financial or other).

Omar Albaroudi declares no potential conflicts of interest (financial or other).

Fares Alahdab declares no potential conflicts of interest (financial or other).

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