Hyperbaric Oxygen for Carbon Monoxide Poisoning

Toxicol Rev 2005; 24 (2): 75-92REVIEW ARTICLE 1176-2551/05/0002-0075/$34.95/0

© 2005 Adis Data Information BV. All rights reserved.

Hyperbaric Oxygen for CarbonMonoxide PoisoningA Systematic Review and Critical Analysis of the Evidence

Nicholas A. Buckley,1 Geoffrey K. Isbister,2,3 Barrie Stokes3 and David N. Juurlink4

1 Department of Clinical Pharmacology and Toxicology, Australian National University Medical School, Canberra,Australian Capital Territory, Australia

2 Emergency Department, Newcastle Mater Hospital, Newcastle, New South Wales, Australia3 Discipline of Clinical Pharmacology, University of Newcastle, Newcastle, New South Wales, Australia4 Departments of Medicine, Pediatrics, and Health Policy, Management, and Evaluation, University of Toronto, Toronto,

Ontario, Canada

ContentsAbstract . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 751. Criteria for Considering Studies for This Review . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 77

1.1 Trial Design . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 771.2 Types of Participants, Intervention and Outcome Measures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 771.3 Search Strategy for Identification of Studies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 771.4 Methods of the Review . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 771.5 Description of Studies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 801.6 Methodological Quality: Allocation Concealment . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 801.7 Pooled Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 80

2. Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 812.1 Heterogeneity and Reconciling Conflicting Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 812.2 Possible Limitations of the Negative Studies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 812.3 Additional Limitations of the Positive Studies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 822.4 Synthesis of Trial Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 842.5 Application of Bayesian Models to Aid Decision Making . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 842.6 Bayesian Meta-Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 85

3. Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 863.1 Implications for Practice . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 863.2 Implications for Research . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 86

Poisoning with carbon monoxide (CO) is an important cause of unintentional and intentional injuryAbstractworldwide. Hyperbaric oxygen (HBO) enhances CO elimination and has been postulated to reduce the incidenceof neurological sequelae. These observations have led some clinicians to use HBO for selected patients with COpoisoning, although there is considerable variability in clinical practice.

This article assesses the effectiveness of HBO compared with normobaric oxygen (NBO) for the preventionof neurological sequelae in patients with acute CO poisoning. The following databases were searched:MEDLINE (1966 to present), EMBASE (1980 to present), and the Controlled Trials Register of the CochraneCollaboration, supplemented by a manual review of bibliographies of identified articles and discussion withrecognised content experts.

All randomised controlled trials involving people acutely poisoned with CO, regardless of severity, wereexamined. The primary analysis included all trials from which data could be extracted. Sensitivity analysis

76 Buckley et al.

examined trials with better validity (defined using the validated instrument of Jadad) and those enrolling moreseverely poisoned patients.

Two reviewers independently extracted from each trial, including information on the number of randomisedpatients, types of participants, the dose and duration of the intervention, and the prevalence of neurologicalsequelae at follow-up. A pooled odds ratio (OR) for the presence of neurological symptoms at 1-monthfollow-up was calculated using a random effects model. Bayesian models were also investigated to illustrate thedegree of certainty about clinical effectiveness.

Eight randomised controlled trials were identified. Two had no evaluable data and were excluded. Theremaining trials were of varying quality and two have been published only as abstracts. The severity of COpoisoning varied among trials. At 1-month follow-up after treatment, sequelae possibly related to CO poisoningwere present in 242 of 761 patients (36.1%) treated with NBO, compared with 259 of 718 patients (31.8%)treated with HBO. Restricting the analysis to the trials with the highest quality scores or those that enrolled allpatients regardless of severity did not change the lack of statistical significance in the outcome of the pooledanalysis. We found empiric evidence of multiple biases that operated to inflate the benefit of HBO in twopositive trials. In contrast, the interpretation of negative trials was hampered by low rates of follow-up, unusualinterventions for control patients and inclusion of less severely poisoned patients. Collectively, these limitationsmay have led negative trials to overlook a real and substantial benefit of HBO (type II error).

There is conflicting evidence regarding the efficacy of HBO treatment for patients with CO poisoning.Methodological shortcomings are evident in all published trials, with empiric evidence of bias in some,particularly those that suggest a benefit of HBO. Bayesian analysis further illustrates the uncertainty about ameaningful clinical benefit. Consequently, firm guidelines regarding the use of HBO for patients with COpoisoning cannot be established. Further research is needed to better define the role of HBO, if any, in thetreatment of CO poisoning. Such research should not exclude patients with severe poisoning, have a primaryoutcome that is clinically meaningful and have oversight from an independent data monitoring and ethicscommittee.

Carbon monoxide (CO) is a colourless, odourless and tasteless Death is rare in patients who reach medical care, and preventiongas generated during the incomplete combustion of carbon-based of permanent neurological damage is the major goal of treatment.compounds.[1] Poisoning with CO is an important cause of unin- Two main syndromes are described after acute CO poisoning: (i)tentional and intentional injury worldwide. In the US alone, an persistent neurological sequelae (PNS); and (ii) delayed neurologi-estimated 1000–2000 accidental deaths due to CO exposure occur cal sequelae (DNS).[1] The former are neuropsychiatric symptomseach year, resulting from an estimated 40 000 exposures.[2] About and/or signs referable to CO poisoning continuously present from6% of these exposures are currently treated with hyperbaric oxy- the time of poisoning, whereas the latter are characterised by agen (HBO) in the US, with the majority receiving a single treat- relapse of symptoms and/or signs referable to CO poisoning after ament.[2] transient period of improvement. The DNS and PNS syndromes

may overlap. Both tend to improve over the first year, althoughThe pathophysiology of CO exposure is complex and incom-long-term neuropsychiatric sequelae remain in a substantial pro-pletely understood. Upon exposure, CO binds to haemoglobinportion of patients, particularly those with abnormal neuroimag-with an affinity 210-times that of oxygen, thereby decreasing theing.[1] The symptoms and signs are not specific to CO poisoning,oxygen-carrying capacity of blood. CO can also produce injury byand range from subtle personality changes, mood disorders andseveral other mechanisms including direct disruption of cellularmemory loss to focal neurological injuries and other severelyoxidative processes, binding to myoglobin and hepatic cyto-disabling manifestations of hypoxic brain injury.chromes, and peroxidation of brain lipids.[1] Most of these effects

lead to tissue hypoxia, varying degrees of end-organ damage, and Standard treatment for CO poisoning includes removal fromoccasionally death. The severity of poisoning is a function of the the site of exposure, administration of supplemental surface pres-duration of exposure, the ambient concentration of CO, and the sure oxygen, general supportive care and occasionally HBO. Theunderlying health status of the exposed individual. Although use- elimination half-life of carboxyhaemoglobin (approximately 320ful for diagnosis when detected, the initial carboxyhaemoglobin minutes) is shortened approximately 5-fold by the administrationlevel correlates poorly with outcome.[3] of 100% oxygen at atmospheric pressure (normobaric oxygen

© 2005 Adis Data Information BV. All rights reserved. Toxicol Rev 2005; 24 (2)

Hyperbaric Oxygen for Carbon Monoxide Poisoning 77

[NBO]).[1] However, no trial has shown that supplemental oxygen sciousness.[10,12] Two trials included all patients with CO poison-improves clinical outcomes, and the optimal duration of treatment ing regardless of severity.[9,13] Two trials included only thoseis not known. patients with no loss of consciousness.[14,15]

The administration of oxygen at pressures higher than atmos- Studies were included where patients with CO poisoning werepheric (HBO) further hastens the elimination of carboxy- randomised to receive HBO (in any regimen) or not to receivehaemoglobin.[1] It was suggested many years ago, based on uncon- HBO. In each instance, virtually all patients received treatmenttrolled clinical studies or comparisons with historical controls, that with NBO prior to randomisation, which would be consideredthe use of HBO prevents the development of PNS and/or DNS.[4-6] standard practice. The duration, timing and dose of both HBO andThese observations have led to widespread use of HBO in the NBO varied substantially among studies (see table I).management of selected patients with CO poisoning, although The main outcome measure of interest was the prevalence ofthere is considerable variability in clinical practice.[2] sequelae at follow-up (ranging from 4 to 6 weeks after randomisa-

Because HBO is available only at certain larger hospitals tion). No universally accepted criteria exist for the diagnosis of(necessitating the transfer of potentially unstable patients) and is PNS or DNS, and these were defined and obtained differently inoccasionally complicated by barotrauma, seizures and claustro- each study. Although it would have been preferable to adopt aphobia, its superiority over NBO in the treatment of CO poisoning common outcome (such as the presence or absence of symptoms atmust be established prior to it being recommended as standard 1-month follow-up), this would have excluded the only sizabletherapy. HBO is also substantially more expensive than NBO. For positive study.[9] Therefore, we preserved the outcome definitionexample 1990s estimates of the cost of establishing a multi-place of each publication, and used the time nearest to 1 month whenchamber are between $US400 000 and $US2 950 000; the cost per multiple assessments were made. However, this is a source oftreatment was estimated to be $US220/session, and additional substantial uncertainty (see section 2.3).operating and transport costs are also incurred.[7]

1.3 Search Strategy for Identification of StudiesA systematic review of HBO in patients with CO poisoning waspublished in 2000, providing a summary estimate of effect using

The search strategy was based on the Cochrane Injuries Groupdata from three of six published studies.[8] Additional research has

search strategy. RCTs, without language restriction, were identi-subsequently been published.[9-11]

fied in a search of the MEDLINE and EMBASE databases (1966This article examines the effectiveness of HBO in reducing the

to present), supplemented with manual searching of the referenceprevalence of neurological symptoms and signs approximately 1

lists of retrieved documents. The electronic search strategy ismonth after treatment in patients with acute CO poisoning.

shown in appendix 1. A search of the Cochrane Controlled TrialsRegister was performed with the assistance of a search strategist1. Criteria for Considering Studies for This Reviewwithin the Injuries Review Group.

Two additional abstracts not identified using the search strate-1.1 Trial Design gies described above were identified by a manual search of refer-

ences of other publications.[10,15] We also identified abstractsThe analysis was limited to randomised controlled trialsdescribing interim analyses of three trials that were eventually(RCTs), with or without blinding. Trials that used surrogate out-published in full.[16-18]

come measures, did not report a frequency of neurological seque-lae, or did not present data allowing the calculation of the frequen-

1.4 Methods of the Reviewcy of neurological sequelae at approximately 1 month were ex-cluded from the analysis. All trials identified with this search strategy have been consid-

ered for inclusion in this review. Several trials of HBO with1.2 Types of Participants, Intervention and

objectives other than treatment of CO poisoning have been exclud-Outcome Measures

ed without further evaluation. One reviewer examined the elec-tronic search results for trials that were possibly relevant, andThe participants were adults acutely poisoned by CO. Allthese articles were retrieved in full.studies excluded pregnant women. The diagnosis of CO poisoning

The quality of each trial was independently assessed by twowas established by a history of exposure to CO and/or an elevatedreviewers according to the method of Jadad et al.[19]carboxyhaemoglobin level. The severity of CO poisoning varied

between the individual trials. Two studies stratified randomisation As there is evidence that the quality of allocation concealmentaccording to whether or not there was a history of loss of con- affects the results of studies,[20] the two reviewers independently


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Table I. Characteristics of included studies

Study Methods Participants Interventions Outcomes Notes

Raphael et Prospective, randomised, 629 adults admitted within 12h Only those without history of Intention-to-treat Allocation concealmental.[12] unblinded trial. Randomisation of termination of CO exposure. LOC (n = 343) randomised to analysis. Outcome B

stratified according to history of Inclusion: age >15y, admitted HBO vs NBO (HBO × 2h measures included self-loss of consciousness. within 12h, COHb >10% followed by 100% O2 × 4h vs assessmentAllocation by sealed opaque (smoker) or 5% (nonsmoker). 100% O2 × 6h). Patients questionnaire andenvelopes, not sequentially Exclusion: other intoxication, without LOC randomised to physical examination bynumbered. Only those with no pregnancy, CV collapse, HBO × 1 vs HBO × 2; not neurologist (nonblinded)history of LOC randomised to pulmonary oedema, non- included in analysis. HBO at 1mo. No differenceHBO vs NBO; more severe feasible HBO (technical regimen: 2h total, including 30 in outcome in patientspatients randomised to different problems etc.), difficulty in min compression and without history of LOCregimens of HBO. Jadad score stratifying into groups A or B decompression, flanking 60 min (NBO 50/1583/5 (by LOC), refusal by patient at 2.0 ATA symptomatic vs HBO

51/159 symptomatic).No deaths or severesequelae in thesepatients

Thom et al.[14] Prospective, randomised, 65 patients referred from local All patients in HBO arm given Outcome assessors not No adjustment fornonblinded trial of HBO vs emergency departments, within 100% O2 until HBO initiated. blind to treatment interim analysis andNBO. Treatment allocation by 6h of removal from exposure. HBO begun within 6h of end of allocation. 5 patients remarkable decision tocomputer-generated random Inclusion: history of acute exposure. HBO at 2.8 ATA for lost to follow-up (2 stop trial just 7 patientsnumbers within sealed opaque exposure, elevated COHb, 30 min, then 2.0 ATA × 90 min. control, 3 HBO). 7/30 later despite NSenvelopes, not sequentially symptoms consistent with CO NBO 100% O2 until all patients in control arm difference at the interimnumbered. Jadad score 3/5 poisoning. Exclusion: history of symptoms resolved (mean 4.2 had DNS vs 0/30 analysis. Allocation

LOC, active ischaemia. Two ± 0.3h). After intervention, patients in HBO arm concealment Bgroups largely similar (higher neuropsychological baselineaverage COHb in HBO group: testing (6 tests) performed24.6% vs 20.0%) (some up to 12h post-Rx).

Occurrence of DNS self-reported as (i) recurrentsymptoms or (ii) new symptomconsistent with DNS, plusdeterioration in one or moresubtest upon retesting

Mathieu et Prospective, randomised, 575 non-comatose patients with HBO at 2.5 ATA for 90 min Neuropsychological Interim report only –al.[15] nonblinded multicentre trial of CO poisoning. Exclusions: (plus 15 min compression and testing at 1mo, 3mo, trial has recently

HBO vs NBO. Randomisation mixed poisoning, pregnancy or 15 min decompression) vs 12h 6mo and 1y. ceased enrollingmethod and allocation HBO contraindication NBO ‘Persistent neurological patients but theconcealment unknown. Jadad manifestations’ in 23% complete data set hasscore 2/5 of HBO arm and 26% not been analysed.

of NBO arm at 1mo. No Allocation concealmentdata on deaths or Bsevere neurologicalinjury

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Table I. Contd

Study Methods Participants Interventions Outcomes Notes

Scheinkestel et Prospective double-blind RCT 230 patients sequentially All patients given high-flow O2 191 randomised (104 Several otheral.[13] of HBO vs NBO. Cluster referred to single centre in prior to randomisation. Daily HBO, NBO 87, conclusions in text,

randomisation for patients Australia. Exclusions (n = 39): treatment (×3) of HBO (100 discrepancy due to based on repeatedpresenting simultaneously. refused consent, children, burn min; 60 min at 2.8 ATA) OR cluster). 3 deaths in neuropsychologicalAllocation through sealed victims, pregnant. Two groups NBO (100 min of 100% O2 at 1 each group. PNS testing. However, noopaque envelopes, not similar for all important ATA) as a sham dive. After diagnosed in 77/104 adjustment for multiplesequentially numbered. Patients variables. 89% male, coma in third treatment, patients with HBO and 59/87 NBO comparisons; highand outcome assessor blind to 50.6%, average COHb 21%. deficits were treated again, with patients. DNS likelihood of spuriousallocation, technicians and Large number of suicide high-flow O2 in between. Three diagnosed in 5/104 statistical significance.nurses not. Stratified by vent/ attempts (69%), co-intoxication additional courses of original HBO and 0/87 NBO. Allocation concealmentnon-vent and suicide vs (44%) and severe poisonings therapy given to 28% HBO and Poor follow-up Baccidental exposure. Jadad (73%) 15% NBO because of ‘poor attendance (46%) atscore 5/5 outcome’ 1mo. 34/52 with

symptoms in HBO armvs 20/34 withsymptoms in NBO arm(NS)

Weaver et al.[9] Prospective, randomised, 152 patients with CO poisoning HBO: 1 session 3 ATM × 1h Repeated Primary outcomedouble-blind trial of HBO vs (symptomatic with COHb >10% and 2 ATM × 1h then 2 neuropsychological altered substantiallyNBO. Randomisation method or symptoms and signs sessions 2 ATM × 2h at 6–12h testing immediately from early descriptionssequentially numbered sealed unequivocally due to CO intervals. NBO: sham treatment after treatments 1 and of trial and interimenvelopes. Jadad score 5/5. exposure). Exclusions: >24h at 1 ATM. O2 not routinely used 3 and at 2, 6, 26 and analysis. AllocationAllocation concealment possibly since exposure, pregnancy, after first session 52wk. ‘Cognitive concealment Bcompromised by fixed block <16y of age, ‘moribund’ or sequelae’ found in 19/size of 6 refused consent. Stratified by 76 HBO and 35/76

LOC, age <40y and delay to NBO patients at 6wk.treatment <6h No deaths. No data on

severe neurologicalinjury

Raphael et Prospective, randomised, 385 adults admitted with Group A: 2 ATM HBO × 1h + Outcome measures Abstract of meetingal.[10] nonblinded trial in patients with accidental CO poisoning. NBO × 4h vs NBO × 6h included self- presentation (not

moderate to severe accidental Detailed inclusion and exclusion Group B: 2 ATM HBO × 1h + assessment interim analysis).CO poisoning. Randomisation criteria not specified. Those NBO × 4h vs 2 sessions of 2 questionnaire and Allocation concealmentstratified according to whether with history of transient loss of ATM HBO × 1h + NBO × 4h physical examination by Bthere was transient LOC only or consciousness (group A) were neurologist (blinded) atpatients were comatose. randomised to HBO (n = 93) vs 1mo. No difference inRandomisation method NBO (n = 86). Comatose primary outcome inunknown. Only those with patients (group B) were group A patientstransient LOC (not comatose) randomised to HBO × 1 vs (symptoms in 29/74randomised to HBO vs NBO; HBO × 2 and are not included NBO and 33/79 HBO).more severe patients in analysis. Patients without No deaths orrandomised to different LOC were excluded neurological signs inregimens of HBO. Jadad score group A patients3/5

ATA = atmospheres absolute (pressure); ATM = atmospheres (pressure); CO = carbon monoxide; COHb = carboxyhaemoglobin; CV = cardiovascular; DNS = delayed neurologicalsequelae; HBO = hyperbaric oxygen; LOC = loss of consciousness; NBO = normobaric oxygen (100%); NS = non-significant; OR = odds ratio; PNS = persistent neurologicalsequelae; RCT = randomised controlled trial; Rx = treatment.

80 Buckley et al.

assessed the quality of each trial according to the method of Schulz but had no control arm and also an insufficient time (2–3 weeks) toet al.[20] as shown below: final follow-up.[11] Two trials were published in abstract form only

and many details are missing, although they meet the essential• A = trials deemed to have taken adequate measures to concealcriteria for inclusion in the review.[10,15]allocation (i.e. centralised randomisation; numbered or coded

All trials with evaluable data were included in the primarybottles or containers; serially numbered, opaque sealed enve-analysis.[9,10,12-15] The severity of CO poisoning and the rates oflopes, etc.);‘neurological sequelae’ varied substantially in the individual trials.• B = trials in which the authors either did not report an allocationReported rates of ‘neurological sequelae’ varied from 0% to 74%concealment approach at all, or reported an approach that didin those receiving HBO and 21% to 67% in those receiving NBO.not fall into one of the other categories;Two studies stratified randomisation according to whether or not• C = trials in which concealment was inadequate (such asthere was a history of loss of consciousness, administering HBO toalternation or reference to case record numbers or to dates ofall patients with impaired consciousness.[10,12] For these studies,birth).only data from the group randomised to NBO or HBO wasWhere the method of allocation concealment was not reported,included in the pooled analysis. A more detailed description ofor where additional information was required to appropriatelythese studies is shown in table I.assess study quality, the principal authors of these trials were

contacted for clarification. However, responses did not uniformly1.6 Methodological Quality: Allocation Concealmentclarify these questions.

When the two reviewers disagreed on either the quality score or In all of the included studies, allocation concealment could notthe adequacy of allocation concealment, agreement was able to be be assured (graded B). The two trials published only in abstract doreached through dialogue and consensus. Data were extracted not record the method.[10,15] Three trials used sealed envelopes, butfrom each trial including information on the participants (age and these were not sequentially numbered.[12-14] The other trial usedsex distribution, mode of poisoning, carboxyhaemoglobin level sequentially numbered sealed envelopes.[9] However, there was aupon randomisation, and history of loss of consciousness), the possibility for a failure of allocation concealment related to fixedinterventions (duration and dose of NBO and HBO), and preva- block sizes if the treating team were aware of previous treatmentlence of signs and symptoms at follow-up. Insufficient data were assignments.[22] Thus, selection bias cannot be excluded in any ofavailable to examine the effect of HBO in any subgroup of the studies. Only one study reported a large difference in baselinepatients. severity.[9] Patients assigned to HBO were less likely than those

A pooled odds ratio (OR) for the dichotomous outcome of given NBO to have cerebellar dysfunction (4% vs 15%; p = 0.03).‘neurological sequelae’ at 1-month follow-up was calculated using They also had a non-significant shorter median exposure to COa random effects model. (4.2 [interquartile range 1.6–8.9 hours] vs 5.0 [2.0–13.5 hours]; p

To explore the relevance and robustness of differences in = 0.2).[23] Each study outlined the numbers of patients lost toclinical outcomes, a number of post hoc Bayesian analyses using follow-up, although the proportion followed up varied widely (seeWinBUGS were also performed. WinBUGS is the windows inter- table I).face for BUGS (Bayesian inference Using Gibbs Sampling),which is a Bayesian statistical modelling system that generates 1.7 Pooled Resultsposterior estimates and credible intervals for all parameters of

The six trial results were not consistent in their results. Theinterest using Markov chain Monte Carlo (MCMC) numericalCochran Q test for heterogeneity was significant (p < 0.03) and thesimulation methods. Further details of the complex methodologyI2 test result was 58.5%, indicating that less than half of thisincluding full analyses are listed in appendix 2 with the WinBUGSvariation in results likely occurs due to chance. These factorscode, input data and initial values.suggest that a random effects method of calculating confidenceintervals is appropriate. Moreover, any pooled analysis of such1.5 Description of Studiesinconsistent studies should be interpreted with caution withoutsome explanation for the heterogeneity.Eleven publications describing eight potentially relevant RCTs

were identified.[9-18,21] One trial was excluded because of inade- Six trials employing different doses of NBO and HBO werequate allocation concealment and the use of surrogate outcome included in the pooled analysis.[9,10,12-15] The severity of COmeasures.[21] Also excluded was another trial (published in ab- poisoning was inconsistent between trials. In these trials, a total ofstract form only) that compared two different regimens of HBO 1479 patients were randomised to treatment with different regi-



mens of NBO and HBO. Of these, symptoms were present at 1month follow-up in 242 of 761 patients (31.8%) treated with HBO,compared with 259 of 718 patients (36.1%) treated with NBO. TheOR for neuropsychiatric symptoms with HBO was 0.77 (95% CI0.51, 1.14). A similar non-significant OR results from meta-analysis of neuropsychiatric sequelae (as defined by the au-thors).[24]

Four trials met the pre-specified criteria for acceptable quali-ty.[9,12-14] Two trials received a quality score of 3/5 on the scale ofJadad et al.[19] In each instance, double-blinding was not possiblebecause control patients did not enter a hyperbaric chamber.[12,14]

The possibility of observer bias in these trials is particularlystrong. The two studies in which double-blinding was performed

0.1 1 10

Pooled

f

e

d

c

b

a

Study

Odds ratio

Fig. 1. Odds ratios (95% confidence intervals) for ‘neurological sequelae’at 4–6 weeks in randomised controlled trials comparing hyperbaric oxygenwith normobaric oxygen treatment. a = Mathieu et al.[15]; b = Raphael etal.[12]; c = Scheinkestel et al.[13]; d = Raphael et al.[10]; e = Weaver et al.[9]; f= Thom et al.[14]

appropriately, received a quality score of 5/5.[9,13] Outcome asses-sors in these trials were blind to treatment allocation.

HBO is driven largely by these discrepant results. It is possible thatA sensitivity analysis was performed by removing the results of these conflicting results relate to significant heterogeneity in the

trials with a Jadad score of <3/5 (these were the two trials pub- patients and treatments studied. It is also possible that this is due tolished in abstract form only) and they may reach an acceptable poor study design and biases in the negative and/or positivelevel of quality when full details are published.[10,15] When the studies.remaining four studies are combined,[9,12-14] a total of 146 of 383

The Jadad assessment of the quality of trials and the Schulzpatients (38%) randomised to HBO had ‘neurological sequelae’ at

approach to grading allocation concealment are widely used in the1 month, compared with 152 of 368 patients (41%) randomised to

Cochrane collaboration. These simple scales are easily used andNBO (OR for neurological sequelae 0.70 [95% CI 0.34, 1.47]).

widely applied, but also disregard many elements of trial qualityWhen restricting the pooling to the two studies that enrolled more

and sources of bias.[25] Detailed analysis of these trials suggest thatseverely poisoned patients[9,13] (the only two studies with a score

some of the most likely sources of error in the negative andof 5/5 on Jadad’s scale), the results remained inconclusive (OR for

positive trials are not identified using the instrument of Jadad.neurological sequelae 0.73 [95% CI 0.22, 2.48]).

After detailed review of the data from these trials, we describefurther methodological problems that may have influenced the2. Discussionresults of each trial.

This systematic review identified six randomised controlled2.2 Possible Limitations of the Negative Studiestrials of HBO versus NBO for the treatment of acute CO poison-

ing.[9,10,12-15] The trials enrolled patients with CO poisoning ofThree common errors unrelated to bias may lead a clinical trialvarying severity, and employed different regimens of HBO and

to erroneously find no benefit from a treatment when one existsNBO. Only two trials[9,13] were conducted with double-blindingFirst, the trial may be too small and have inadequate power tothrough sham treatment. The pooled analysis demonstrates nodetect a statistically (and possibly clinically) significant differencesignificant difference in the prevalence of neurological sequelae atin outcomes. Secondly, the chosen primary outcome may not have1 month after therapy for patients treated with NBO or HBO. Thisbeen appropriate, either because of loss to follow-up, inaccuracywas also true in sensitivity analyses restricted to the trials with thein definition or measurement of the outcome, or because thehighest Jadad score or those that enrolled severely poisoned pa-outcome of interest occurred too infrequently (also leading totients – those most likely to derive benefit from an intervention.inadequate power). Finally, the intervention used in the study mayhave been sub-optimal, for example there was too high or too low2.1 Heterogeneity and Reconciling Conflicting Dataa ‘dose’ or duration of therapy. If we examine the ‘negative’ trials

It is apparent that there are two studies showing a very large from this perspective, the first seems unlikely, these were the foureffect of HBO and four studies showing minor or no effect (figure largest trials and had 99% power to detect differences of 7–10% in1). The I2 test indicates over half the observed variation is proba- the primary outcome (contrast this with the 21% difference ob-bly not due to chance, and the test for heterogeneity is also served in the two positive studies). However, the other twosignificant (p = 0.03). The ongoing debate about the efficacy of problems are apparent.


82 Buckley et al.

The studies by Raphael et al.[10,12] only randomised patients 2.3 Additional Limitations of the Positive Studies

with less serious poisoning (no loss or transient loss of conscious-

ness, respectively) to treatment with either HBO or NBO. These There are many potential biases that may alter the reportedpatients had few serious adverse outcomes, with the overwhelming outcomes in RCTs. Those with the most empiric evidence for an

influence on treatment effect have been included in the measuresmajority returning to work within 1 month. While this findingof quality we have used.[25] A further common problem that hassuggests that treatment is likely not warranted in these subgroups,been highlighted in recent years is that of bias introduced in theit does not permit inferences to be drawn about the effect of HBOanalysis, interpretation and reporting of trials.[32-34] For example, itin more severely poisoned patients. In general, more seriously illis very common for different outcomes other than those originallypatients are more likely to experience benefit from an efficaciousproposed to be reported as a primary outcome. Such post hoctherapy.analyses introduce a significant possibility of bias and yet are

The RCT of Mathieu et al.[15] is reported only as an interim generally not discoverable from the published paper.[32] A similaranalysis in abstract form. Many details are missing including the but more readily detectable interpretive bias can result from selec-definition of the primary outcome as well as rates of attrition. tive citation of results.[33] This is evident in many reviews thatAlthough the incidence of persistent neurological sequelae at 3 characterise the RCT of Mathieu et al.[15] as showing a benefit ofmonths was significantly lower in patients treated with HBO (5% HBO based on outcomes at 3 months.[26] Post hoc analyses select-vs 15%; p = 0.016), no difference was evident at 1 month, 6 ing those outcomes with the largest difference in the trial willmonths, or 1 year after discharge. Had the investigators adjusted greatly exaggerate the apparent effect size.[35] If such an outcome

is presented as if it were the original primary outcome, thentheir analysis for multiple comparisons, no significant differencestatistical adjustment for multiple unpublished analyses are notbetween treatments would have been identified at any interval.[26]

made. Nor is there an opportunity for readers to consider the biasesThis trial also excluded the most severely poisoned patients (thosethat may be introduced in this process.[36]

who were comatose), thereby jeopardising its ability to detect anIn the trial by Thom et al.,[14] bias may have been introduced inimportant treatment effect.

the randomisation process (through failure of allocation conceal-The study by Scheinkestel et al.[13] is the only negative study

ment) and in assessment of neurological sequelae (the assessmentthat randomised patients with all degrees of severity of CO poison-

was done by nonblinded clinicians who had been on record foring. The main flaw in this study that might have lead to a false many years in support of HBO for CO poisoning).[6] However, it isnegative result was some form of attrition bias. Only 46% of those only apparent from reading the interim report that there was also arandomised were successfully followed up 4–6 weeks later. If the strong possibility of bias introduced in the decision to terminateoutcomes in those lost to follow-up differed systematically from the trial. The trial was stopped at 65 patients and produced athose included in the final analysis (e.g. more or less likely to have statistically significant result. However, an interim analysis at 58neurological sequelae) then this may have reduced any observed patients showed no statistically significant difference. The resultsdifferences between groups.[27] The primary outcome of ‘neuro- of the interim (4/29 vs 0/29 patients with neurological sequelae in

the NBO and HBO arms, respectively) and final analyses (7/32 vslogical sequelae’ was not based on this smaller group that was0/33) show the addition of three patients to the NBO arm (all offollowed up for 1 month, but rather on the neuropsychological testwhom developed neurological sequelae) between the interim andresults at the completion of treatment. Consequently, this trial doesfinal analyses and four patients to the HBO arm (none of whomnot exclude a benefit from HBO at later timepoints.developed neurological sequelae). Termination of the trial at this

The study by Scheinkestel et al.[13] employed cluster randomis-point greatly exaggerated the treatment effect compared with the

ation, which may increase the possibility of bias.[28] However, thisinterim analysis and resulted in a statistically significant difference

criticism has been largely refuted by a subsequent analysis exclud- between treatments. As with the trial of Mathieu et al.,[15] hading patients randomised as part of a cluster.[29] Another valid adjustment for multiple comparisons been performed, no signifi-criticism is that patients in both arms of the trial were treated with cant difference would have been identified.continuous NBO for at least 3 days, which is not standard treat- Similar concerns about post hoc analysis are raised by examin-ment anywhere.[30,31] However, for this anomalous treatment of ing the interim report and other preceding descriptions of Weavercontrol patients to explain why no benefit was observed with HBO et al.’s trial.[18,26,37,38] The report of this double-blind RCT impliesrequires a speculative ‘rescue hypothesis’ about the beneficial (or everything possible has been done to eliminate observer bias.[9]

adverse) effects of 3 days of NBO. However, blinding was only applied to the patients, technicians



and those conducting the neuropsychological tests. The investiga-tors and the statistician were effectively unblinded at the time ofthe interim analysis (if not earlier) when a substantial number ofpatients in one arm of the trial were noted to be intolerant of thehyperbaric chamber (4/25 vs 1/25).[18]

Disproportionate numbers of patients with cerebellar problemsentered one arm of the Weaver trial. As would be expected,neurological sequelae occurred much more commonly if therewere cerebellar signs at the time of enrolment into the study. Thiswas particularly so because two of the six neuropsychiatric testsinvolved ‘trail-making’, which would be affected by even minordegrees of cerebellar dysfunction. It is not possible to determine ifthis occurred due to chance or indicates a failure of truly randomallocation. This imbalance alone could have accounted for half theactual observed difference between the groups, because absolutedifference between arms was 16 individuals, yet there were eightmore individuals with cerebellar dysfunction and neurological

0

10

20

30

40

50

60

70

Digitspan

Trailmaking A

Trailmaking B

Digitsymbol

Blockdesign

Storyrecall

HBO

NBO

T s

core

Fig. 2. Neuropsychological test T scores (population norm is 50, normalrange shown by horizontal lines) and standard deviations at 6 weeks (timeof primary outcome) in the study by Weaver et al.[9] HBO = hyperbaricoxygen; NBO = normobaric oxygen.sequelae in the NBO group. More importantly, this contributed to

an imbalance that meant the results of the trial would vary quitedata on this outcome were presented, and cognitive neurologicalsubstantially for different outcome measures. In that context, it is asequelae (previously specified as a secondary outcome[38]) wereconcern that the primary outcome presented in the final publishedreported instead.[9]

report differs in three respects from that described by the leadThirdly, the ‘intention to treat’ (ITT) analyses assumed thatauthor previously and used in the interim analysis.[9,18,26,37,38]

patients lost to follow-up had neurological sequelae. In the HBOThese differences are characterised in the paragraphs below.group, only one patient was lost to follow-up at the 6-week stageFirst, the clinical definition of ‘neurological sequelae’ changed.compared with four in the NBO group. Thus, this assumptionThree different definitions of neurological sequelae for this RCTfavoured the HBO group and inflated the difference betweenhave been described by the lead author.[9,26,37,38] The first of thesegroups by three individuals. The approach used by Weaver et al.[9]

published in 1995 used different cut-off values for neuropsychia-is in contrast to the standard ITT approach of carrying the lasttric test scores and did not include symptoms as an indicator ofobservation forward.neurological sequelae, both of which are in direct conflict with the

Collectively, the unbalanced recruitment and changed primaryfinal publication. The difference in the primary outcome reportedoutcome engender considerable uncertainty about the conclusionsin the final publication appears to be largely due to a difference inof this trial. The difference in neurological sequelae between theself-reported symptoms.[9] For example, ‘cognitive sequelae’ werearms favoured HBO by just 16 patients. The study’s conclusionsdeemed present if any of three criteria were met. The mostare very sensitive to small changes in event rates; a change in theprobable was the combination of self-reported ‘difficulties withstatus of only four individuals would be sufficient to render thememory, attention or concentration’ (present in >50% of theresults non-significant at the 0.05 level. The post hoc change of thecontrol group but much lower in the HBO group) and a score 1SDdefinition of the primary outcome in three respects could easilybelow normal in any one of six neuropsychological subtests,account for a difference much larger than that. The ITT assump-which might be expected to occur in two-thirds of healthy peopletion alone nearly changes the trial from significant to non-signifi-(p = 1 – [5/6]6). The absolute numbers of those with self-reportedcant.symptoms and ‘cognitive sequelae’ are very similar. In contrast,

there is little difference in the mean scores of the two treatment In summary, the original primary outcome of Weaver etgroups on the objective measures (figure 2). al.’s[18,37] trial was delayed neurological sequelae defined by strin-

Secondly, the primary outcome changed from ‘delayed’ to gent clinical criteria and no ITT assumption. It seems likely from‘total’ neurological sequelae. In the interim analysis, the statistical looking at other outcomes that this trial would show no significanttest of significance was applied to delayed neurological seque- benefit on this outcome.[9] There was no significant differences inlae,[18] using unambiguous criteria clearly defined in 1995 as the functional outcomes (e.g. activities of daily living) or in long-termprimary outcome of the trial.[38] However, in the final paper, no outcomes. Moreover, the mean performance of patients in the


84 Buckley et al.

NBO group was normal for five of the six neuropsychiatric tests, tion. This suggests that the most severely affected patients areand above normal in the sixth (figure 2), suggesting significant likely to have the greatest potential to derive a large enoughimpairment was fairly uncommon and that the majority of those benefit to warrant the risks and expense of such interventions. Noassessed as having neurological sequelae would have been as- significant long-term functional differences in outcome have beensessed as normal by other objective criteria. It is debatable how we shown in any of the studies. Yet, if even a minor benefit could beshould incorporate data from such a post hoc analysis in a pooled proven in terms of such outcomes, the treatment may be worth-analysis,[35] but unfortunately the originally intended primary out- while and cost effective.come has not been reported even as a secondary analysis.

2.5 Application of Bayesian Models to AidDecision Making

2.4 Synthesis of Trial Results

The focus on just one (quite variable) primary outcome of eachIt is apparent that there is considerable room for type II error in trial ignores other potentially more important benefits and also all

the negative trials due to exclusion of high-risk patients, insensi- risks and expenses associated with this treatment. A small differ-tive outcome measures or, in particular, incomplete follow-up. The ence in a very important outcome might be a much better justifica-two positive trials appear to have been influenced by bias at tion for using an expensive or hazardous treatment than a largeseveral stages, suggesting that their results cannot be easily inter- improvement in another outcome. The current situation regardingpreted. Any attempt to pool results from such heterogeneous trials the evidence for HBO treatment might be represented by a graphto provide a common summary measure of outcome should be of probabilities for benefit or harm (figure 3). There is a small butviewed with some scepticism, since all trials had very different substantial possibility the treatment is harmful. There is a substan-interventions, populations and outcome measures. Moreover, no tial possibility that the treatment is beneficial. However, perhapsprovision is made in such meta-analyses for the likely direction of the most likely scenario (from the evidence of RCTs) is that thebias or measurement error in each trial. Even so, pooling all treatment benefits do not justify the expense and risks of thisstudies using a random effects model gives a very wide confidence treatment. In other words, it is not sufficient to have an OR <1 forinterval (OR for neurological sequelae 0.77 [95% CI 0.51, 1.14]), any outcome (e.g. ‘neurological sequelae’) to state that a treatmentconceding a possibility of harm from HBO treatment but, at the is both beneficial and worthwhile; there is another threshold (D)same time, leaving room for the possibility of a substantial benefit for improvements where the potential harms and cost are clearlyin reducing ‘neurological sequelae’. However, the definitions ofneurological sequelae used in studies showing favourable effectsmake it hard to estimate the probable clinical benefit from thistreatment. For example, there are small but significant risks ofHBO treatment, which are increased substantially if there is a needfor transfer to a facility that has a chamber. There are alsoopportunity costs in other areas of the health system from thedecision to purchase, maintain and use this very expensive equip-ment. It is difficult to make a strong case for putting healthresources into HBO, when in the trial that showed the largestdifference, the mean neuropsychological test results at 6 weeksafter poisoning in those randomised to NBO were within thenormal range. If the outcomes recorded had been consistent inusing pre-defined objective criteria for at least one reported out-come, then the shortcomings of the evidence might be informed bymeta-analysis. Presently, the pooled result should be discounted infavour of the recognition that the quality of all existing studies isinadequate to provide firm conclusions about the effectiveness ofHBO.

For this reason, future studies should focus on objective crite-ria. In the trials of Raphael et al.,[10,12] objective neurologicalsequelae were restricted to those who were comatose on presenta-

0.5 1.0 1.5D

HBOharmful

HBObenefits do

not outweighrisk or

expense

HBObeneficial

Less More

Odds ratio for symptoms

Pro

babi

lity

Fig. 3. Probability of temporary neuropsychiatric symptoms with hyperbaricoxygen (HBO) treatment compared with standard treatment and implica-tions for decision making after incorporating an arbitrary threshold (D) toaccount for risks and expense.



the outcome used in the trials (the presence of symptoms at1-month follow-up). This estimates the OR for neurological se-quelae to be 0.74 (0.36–1.1) [median with 2.5% and 97.5% credi-ble limits].

We arbitrarily (and perhaps generously) postulated that a num-ber needed to treat (NNT) of <20 (or >5% absolute reduction inrisk) would indicate a clinically meaningful effect on this subjec-tive outcome. The background event rate was calculated to be 0.33(inverse variance pooled control arm rates from all six trials).Therefore, the threshold (D) for a clinically meaningful effect inthis analysis occurs at an OR of 0.79. The probability that the ORwould be >0.79 (and the NNT <20) was 0.644. This was derivedby generating the posterior distribution curve of the OR (figure 5).Therefore, the chance of a clinically meaningful benefit from HBOis not much better than 0.5 (even chance).

Secondly, we used a Bayesian approach to estimate the effec-tiveness of HBO on the presence of neurological sequelae at 12months. Data were only available for two trials.[9,15] A total of 703

0.5 1.51

HBOharmful

HBObenefits do

not outweighrisk or

expense

HBObeneficial

DOdds ratio for death

Less with HBO More with HBO

Pro

babi

lity

Fig. 4. Probability of death with hyperbaric oxygen (HBO) treatment com-pared with standard treatment and implications for decision making afterincorporating an arbitrary threshold (D) to account for risks and expense.

patients were included, 128 patients followed up at 12 months inthe trial by Weaver et al.[9] and the 575 patients in the Mathieu et

offset. This threshold is very close to 1 for important outcomesal.[15] trial. Neurological sequelae were reported at 12 months in 22

such as long-term neurological damage and death. For example, aof 361 patients (6.1%) treated with HBO, compared with 32 of 342

reduction of a few percent in the absolute risk of disabling neuro-patients (9.4%) treated with NBO. The OR for neurological seque-

logical injury or death could readily justify widespread use of alae with HBO was 0.63 (0.0–1.91) [median with 2.5% and 97.5%very hazardous and expensive treatment (e.g. thrombolytic therapycredible limits] – see appendix 2 for full details. These datafor acute stroke). This threshold is much higher for other outcomes

– temporary, subjective symptoms that do not interfere with activi-ties of daily living. Unfortunately, all of these trials have used suchoutcomes as their primary outcome, and have been grossly un-derpowered to detect differences in objective neurological injuryor death. For example, if we construct a curve of the probabilitiesfor the effect of HBO on death from the trial data (figure 4), wefind that almost any realistic effect of HBO is roughly equallyprobable. For this outcome, the threshold for D is close to 1 but wedo not have the evidence to make this decision anything better thana guess. A similarly unhelpful probability curve would be ex-pected for all clinically meaningful outcomes based on the currentevidence.

2.6 Bayesian Meta-Analysis

To illustrate the application of these principles to the trial data,two analyses were done using WinBUGS on the data taken fromthe six trials.[9,10,12-15] The methods are complex but full analysesare included in appendix 2 with the WinBUGS code, input dataand initial values.

The first analysis included the 1479 patients randomised todifferent regimens of NBO and HBO and examined the effect on

Pr(OR < 0.79 | data) = 0.64

0.0 1.0 2.01.50.5

Odds ratio

Fig. 5. The posterior distribution of odds ratio (OR) generated byWinBUGS. The light and dark shaded areas together indicate the posteriorprobability (Pr) that OR is <1 (favouring hyperbaric oxygen), which is 0.94.The dark shaded area represents the Pr that OR is <0.79, as indicated. AnOR <0.79 is required if the number needed to treat is to be <20.


86 Buckley et al.

NHMRC Clinical Career Development Award ID300785. The authors haveindicate a very high degree of uncertainty about the effects ofno conflicts of interest.HBO on long-term outcomes.

3. Conclusions

3.1 Implications for Practice

CO is the leading cause of poisoning-related death and morbidi-ty in the developed world. Despite several RCTs, the role of HBOremains unclear and the weight of the available evidence neitherconfirms nor refutes a clinically meaningful net benefit.

3.2 Implications for Research

Each of the published trials had easily identifiable flaws thatmight have been averted with more careful planning, more re-sources and trial registration. We suggest a large, well designed,externally audited multicentre trial comparing HBO with NBO isnecessary to examine clinically important outcomes following COpoisoning. We believe it is ethical to enrol people in such a trialbecause no trials published to date report a clinically significantbenefit of HBO using objective and pre-specified outcomes. In-deed, the most severely poisoned patients are particularly impor-tant to enrol in such a study. To eliminate several sources of bias,future studies should employ a double-blind technique using shamdives in a hyperbaric chamber for control subjects. Clinicallyrelevant outcomes should be studied, while multiple hypothesistesting should be minimised unless these analyses are pre-speci-fied and accompanied by appropriate statistical adjustment toavoid inflation of the type I error rate. Any interim analysis shouldbe done by an independent data safety monitoring committee toprevent inadvertent unblinding of clinical investigators. Finally,the trial should be registered to help future systematic reviews toensure all relevant outcomes are reported and to avoid publicationbias.[39]

The most significant barriers to the implementation of such atrial will be the cost and ethical concerns about a control arm giventhe positive results from two trials, particularly that of Weaver etal.[9] The current spending on HBO treatment for CO poisoning islikely to greatly exceed the costs associated with a multicentretrial. A systematic review of the evidence provides support for astate of therapeutic equipoise that warrants ethical approval of awell designed trial.

Acknowledgements

Parts of this review have been published as a Cochrane review (seeJuurlink et al.[24]). David Juurlink is supported by a New Investigator Awardfrom the Canadian Institutes of Health Research, and by the University ofToronto Drug Safety Research Group. Geoffrey Isbister is supported by an

Appendix 1

Search strategy for RCTs on HBO in CO poisoning.

Using OVID and MEDLINE (1966−August 2004):

1. exp carbon monoxide/

2. exp CO/

3. monoxide.tw.

4. 1 or 2 or 3

5. exp hyperbaric oxygen/

6. hyperbaric.tw.

7. 4 and (5 or 6)

8. clinical trial.pt.

9. 7 and 8

Appendix 2

Details of the Bayesian meta-analysis including WinBUGS

code, input data, prior estimates and results.

Analysis 1

The same data used in the conventional meta-analysis from the

six trials listed in figure 1 were included. This included 1479

patients randomised to different regimens of NBO and HBO −

with data on the presence of symptoms at 1-month follow-up.

The initial values required by WinBUGS for all random variables

being estimated were the means of any diffuse priors specified

in the model.

The complete table of results and WinBUGS code, input data

and initial values are shown.

EMBASE (January 1980–August 2004) was searched using

the following strategy:

1. monox* (in ti, ab, kwds)

2. CO (in ti, ab, kwds)

3. or /1-2

4. hyperbar* (in ti, ab, kwds)

5. HBO (in ti, ab, kwds)

6. or /4-5

7. 3 and 6

8. controlled trial (in kmajor, kminor)

9. 7 and 8



WinBUGS code

## standard exact binomial model for odds ratio meta-analysis## taken directly from "Blocker: random effects meta-analysis of## clinical trials" example in WinBUGS Examples, Volume I.## Additional code integrates the OddsRatio posterior, and## estimates the NNT conditional on an inverse-variance pooled event## rate for control arms.

model{ for( i in 1 : Num ) { rc[i] ~ dbin(pc[i], nc[i]) ## exact binomial model for control arms rt[i] ~ dbin(pt[i], nt[i]) ## exact binomial model for test arms logit(pc[i]) <- mu[i] ## logit transformation for p.success in ## control arms (NBO) logit(pt[i]) <- mu[i] + delta[i] ## logit transformation for p.success in ## test arms (HBO); delta's are log odds ratios mu[i] ~ dnorm(0.0,1.0E-8) ## vague priors for mu's delta[i] ~ dnorm(d, tau) ## normal prior for log odds ratios ## (i.e., random effect model) OR[i] <- exp(delta[i]) ## recover the individual trial odds ratios w[i] <- nc[i] / (pc[i]*(1-pc[i])) ## inverse variance weights for pc[i] pcw[i] <- w[i]*pc[i] ## a needed product } d ~ dnorm(0.0,1.0E-2) ## vague normal prior for mean of random ## effect distribution (meta log OddsRatio) tau ~ dgamma(0.001,0.001) ## vague inverse gamma for variance of ## random effect distribution delta.new ~ dnorm(d, tau) ## delta.new is drawn from posterior ## distribution of random effect; it predicts ## a new log OddsRatio OR.new <- exp(delta.new) ## recover predicted new OddsRatio sigma <- 1 / sqrt(tau) ## recover variance of r.e from precision OddsRatio <- exp(d) ## recover meta OddsRatio from meta log OddsRatio; ## meta OddsRatio < 1 favours HBO, since events are ## adverse pooled.pc <- sum(pcw[]) / sum(w[]) ## inverse variance pooled pc ## NNT conditional on pooled pc and OddsRatio nnt <- (1 + pooled.pc*(OddsRatio-1))/(pooled.pc*(pooled.pc-1)*(OddsRatio-1)) pr.nnt0to20 <- step(nnt-0) - step(nnt-20) ## Pr(0 < NNT < 20 | pooled pc and OddsRatio) sig.OR <- step(-(OddsRatio-1)) ## posterior prob OddsRatio < 1 sig.OR79 <- step(-(OddsRatio-0.790187)) ## posterior prob OddsRatio < 0.790187 sig.d <- step(-(d-0)) ## posterior prob d < 0}

This WinBUGS code is essentially identical to that supplied as one of the extensive examples supplied with WinBUGS. We have indented the code, and included brief comments (a '#' separates comment from code), to indicate the program structure and purpose of each code line. Note that we have twice used the step() function to determine the proportion of estimation steps giving, for example, a value of OR (the variable oddsRatio) <1 and <0.79. This is equivalent to a numerical integration under the posterior distribution curve for oddsRatio, allowing the calculation of the posterior probability that the OR is in a certain range.


88 Buckley et al.

This is the form in which the data was input to WinBUGS, with rt and nt being the event counts and Ns for the test (HBO) arms of the 6 trials, and rc and nc similarly forthe control (NBO) arms.

Data

list(## Schei Mathieu Raph89 Thom Weaver Raph04rt = c( 30, 69, 51, 0, 19, 33),nt = c( 48, 299, 159, 30, 76, 79),

rc = c( 25, 73, 50, 7, 35, 29),nc = c( 40, 276, 148, 30, 76, 74),

Num = 6)

WinBUGS requires initial values for all random variables being estimated from the data. The standard practice is to use the means of any diffuse priors specified in themodel.

Inits

list(d = 0, ## mean of r.e. distributiondelta.new = 0, ## predicted new effecttau = 1, ## initial value for dgamma(0.001,0.001) priormu = c(0,0,0,0,0,0),## initial value s for dnorm(0.0,1.0E-8) priordelta = c(0,0,0,0,0,0) ## initial value for dnorm(d, tau) prior)

WinBUGS reports on any variables of interest, giving both posterior means and medians, and the 2.5 and 97.5 percentage points of posterior distributions.

WinBUGS can produce plots of posterior distributions. This is the raw graphic generated by WinBUGS for log OR. Figure 5 is a smoothed and shaded version of this figure using Microsoft® Paint.

Table of Results

node mean sdMC

error2.5% median 97.5% start sample

OddsRatio 0.7481 0.2196 0.005516 0.3702 0.7417 1.108 1001 5000

nnt 60.62 3026.0 42.98 -62.76 14.88 125.3 1001 5000

pr.nnt0to20 0.6248 0.4842 0.01625 0.0 1.0 1.0 1001 5000

sig.OR 0.9426 0.2326 0.005997 0.0 1.0 1.0 1001 5000

sig.OR79 0.637 0.4809 0.01595 0.0 1.0 1.0 1001 5000

d sample: 3500

Posterior of log OR

−10.0 −5.0 0.0 5.0 10.0



The Mathematica calculations supporting the use of an OR threshold of 0.790187 for an NNT of 20, when the background event rate is found via an inverse variancepooling of control arm rates from all six trials, giving 0.332.

Section 1p1 = 0.185;p2 = 0.058;

OR =

0.271246

NNT =

7.87402

What must p2 be, if the threshold NNT is 20?Clear[p1, p2, OR]

so1 = Solve[ == 20, p2][[1]]//Simplify

{p2→ − + p1}

A check of this solution...p1−p2/.sol

What is the general odds ratio in this case?

What is the odds ratio in this case (i.e., with p1 = 0.185)?

/.sol/.{p1→0.185}

0.687549

We have 6 trials with control arm Data...rc = {25, 73, 50, 7, 35, 29};nc = {40, 276, 148, 30, 76, 74};

rates = //N

{0.625, 0.264493, 0.337838, 0.233333, 0.460526, 0.391892}

crudePooledRate = //N

0.340062

For a pooled estimate of the control event rate, we weight by inverse variances...

weights = { }−1

{170.667, 1418.76, 661.59, 167.702, 305.907, 310.516}

thresholdRate =

0.331822

thresholdOR = /.sol/. {p1→thresholdRate}

0.790187

p2(1-p2) p1(1−p1)

p2(1-p2) p1(1−p1)

p2(1−p2) p1(1−p1)

p2(1−p2) p1(1−p1)

(−1+p1)(−1+20p1) p1(−21+20p1)

1p1−p2

120

120

rcnc

Plus @@ rcPlus @@ nc

rates ×(1-rates) nc

Plus @@(rates × weights) Plus @@ weights

1p1−p2

/.sol//simplify


90 Buckley et al.

Analysis 2We also used WinBUGS to estimate the effectiveness of HBO on the presence of neurological sequelae at 12 months. Data were only available for two trials (Weaver et al. and Mathieu et al.) A total of 703 patients were included, 128 patients followed up at 12 months in the trial by Weaver et al. and the 575 patients in the Mathieu et al. trial. Neurological sequelae were reported at 12 months in 22 of 361 patients (6.1%) treated with HBO, compared with 32 of 342 patients (9.4%) treated with NBO. The OR for neurological sequelae with HBO was 0.63 (0.0 to 1.91) [median with 2.5% and 97.5% credible limits].

The complete table of results and WinBUGS code, input data and initial values are shown below.

WinBUGS code

## standard exact binomial model for odds ratio meta-analysis## taken directly from "Blocker: random effects meta-analysis of## clinical trials" example in WinBUGS Examples, Volume I.## Additional code integrates the OddsRatio posterior, and## estimates the NNT conditional on an inverse variance pooled event## rate for control arms.

model{ for( i in 1 : Num ) { rc[i] ~ dbin(pc[i], nc[i]) ## exact binomial model for control arms rt[i] ~ dbin(pt[i], nt[i]) ## exact binomial model for test arms logit(pc[i]) <- mu[i] ## logit transformation for p.success in ## control arms (NBO) logit(pt[i]) <- mu[i] + delta[i] ## logit transformation for p.success in ## test arms (HBO); delta's are log odds ratios mu[i] ~ dnorm(0.0,1.0E-8) ## vague priors for mu's delta[i] ~ dnorm(d, tau) ## normal prior for log odds ratios ## (i.e., random effect model) OR[i] <- exp(delta[i]) ## recover the individual trial odds ratios w[i] <- nc[i] / (pc[i]*(1-pc[i])) ## inverse variance weights for pc[i] pcw[i] <- w[i]*pc[i] ## a needed product } d ~ dnorm(0.0,1.0E-2) ## vague normal prior for mean of random ## effect distribution (meta log OddsRatio) tau ~ dgamma(0.001,0.001) ## vague inverse gamma for variance of ## random effect distribution delta.new ~ dnorm(d, tau) ## delta.new is drawn from posterior ## distribution of random effect; it predicts ## a new log OddsRatio OR.new <- exp(delta.new) ## recover predicted new OddsRatio sigma <- 1 / sqrt(tau) ## recover variance of r.e from precision OddsRatio <- exp(d) ## recover meta OddsRatio from meta log OddsRatio; ## meta OddsRatio < 1 favours HBO, since events are ## adverse pooled.pc <- sum(pcw[]) / sum(w[]) ## inverse variance pooled pc

## NNT conditional on pooled pc and OddsRatio nnt <- (1 + pooled.pc*(OddsRatio-1))/(pooled.pc*(pooled.pc-1)*(OddsRatio-1)) pr.nnt0to20 <- step(nnt-0) - step(nnt-20) ## Pr(0 < NNT < 20 | pooled pc and OddsRatio) sig.OR <- step(-(OddsRatio-1)) ## posterior prob OddsRatio < 1}

Data

list(## Mathieu Weaverrt = c( 13, 9 ), ##total 22 = 0.0609418nt = c( 299, 62 ), ##total 361

rc = c( 14, 18 ), ##total 32 = 0.0935673nc = c( 276, 66 ), ##total 342

Num = 2)



The exact 95% CI for the OR is [0.106205, 4.03562] with length 3.92942. The 95% bCredI is (0.0, 1.91) with length 1.91. Thus, the length of the 95% bCredI is 0.486077 of the length of the 95% CI. This happens when there is nontrivial skewness in the distribution. However, it is a lot more computation to obtain the shortest 95% containing interval than it is to just drop 2.5% off either end of a sorted list.

The pooled point estimates for HBO, 0.0609418, and NBO, 0.0935673 lead to an NNT of 30.65, which is pleasingly consistent with the WinBUGS median of theposterior NNT of 32.47. However as the WinBUGS integration under the posterior shows, the posterior probability that NNT is between 0 and 20 is only 0.0964.

Table of Results

node mean sdMC

error 2.5% median 97.5% start sample

OddsRatio 45.42 1519.0 21.1 0.1064 0.6308 4.036 1001 5000

nnt 218.4 14790.0 210.2 -286.1 32.47 329.3 1001 5000

pooled.pc 0.06678 0.01473 3.593E-4 0.04037 0.066 0.09825 1001 5000

pr.nnt0to20 0.0964 0.2951 0.006971 0.0 0.0 1.0 1001 5000

Pr(OR<1|data) 0.8478 0.3592 0.00921 0.0 1.0 1.0 1001 5000

This is the posterior distribution for NNT

95% Bayesian credible interval

−400 −200 0 200 400 6000

500

1000

1500

2000

2500


92 Buckley et al.

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Hyperbaric Oxygen for Carbon Monoxide Poisoning