Beclometasone for chronic obstructive pulmonary disease

Abstract

Background

Chronic obstructive pulmonary disease (COPD) is a chronic obstructive lung condition, diagnosed in patients with dyspnoea, chronic cough or sputum production and/or a history of risk factor exposure, if their postbronchodilator forced expiratory lung volume in 1 second (FEV₁)/forced vital lung capacity (FVC) ratio is less than 0.70, according to the international GOLD (Global Initiative for Obstructive Lung Disease) criteria.

Inhaled corticosteroid (ICS) medications are now recommended for COPD only in combination treatment with long‐acting beta₂‐agonists (LABAs), and only for patients of GOLD stage 3 and stage 4 severity, for both GOLD groups C and D.

ICS are expensive and how effective they are is a topic of controversy, particularly in relation to their adverse effects (pneumonia), which may be linked to more potent ICS. It is unclear whether beclometasone dipropionate (BDP), an unlicensed but widely used inhaled steroid, is a safe and effective alternative to other ICS.

Objectives

To determine the effectiveness and safety in COPD of inhaled beclometasone alone compared with placebo, and of inhaled beclometasone in combination with LABAs compared with LABAs alone.

Search methods

We searched the Cochrane Airways Group Specialised Register of trials (CAGR) (includes Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, EMBASE, CINAHL, AMED and PsycINFO, and handsearching of respiratory journals and meeting abstracts) (February 2013), conference abstracts, ongoing studies and reference lists of articles. We contacted pharmaceutical companies and drug marketing authorisation bodies/ethics committees in 49 countries and obtained licensing information.

Selection criteria

Randomised controlled trials of BDP compared with placebo, or BDP/LABA compared with LABA, in stable COPD. Minimum trial duration is 12 weeks.

Data collection and analysis

Inclusion, bias assessment and data extraction were conducted by two review authors independently. The analysis was performed by one review author. Study authors were contacted to obtain missing information.

Main results

For BDP versus placebo, two studies were included, of which one trial (participants n = 194) was included in the quantitative analysis. This study was a very high‐dose trial with stable stage 2 and 3 COPD participants. No statistically significant results in change in lung function, mortality, exacerbations, dyspnoea scores or withdrawal were obtained. The quality of the evidence of all these outcomes was graded low to very low. Data on risk of pneumonia were lacking.

The main focus of the review was the more clinically relevant BDP/LABA versus LABA arm. Therefore the findings are reported more fully.

For BDP/LABA versus LABA, one study (n = 474) was included, with a further ongoing study identified for future inclusion. The included trial was a high‐dose study of stable stage 3 COPD participants. Compared with LABA, people receiving BDP/LABA showed a statistically significant improvement in FEV₁ lung function measurements of 0.051 L (95% confidence Interval (CI) 0.001 to 0.102, P = 0.046) (high quality of evidence) and in (self‐reported) days without rescue bronchodilators (mean difference 7.05, 95% CI 0.84 to 13.26, P = 0.03) (low quality), both of which are unlikely to be clinically significant. Participants receiving BDP/LABA also had a statistically significant increased rate of exacerbations leading to hospitalisation (risk ratio (RR) 1.84, 95% CI 1.17 to 2.90, P = 0.008) (moderate quality), although this finding is debatable as this study's post hoc analysis showed no statistically significant difference when accounting for country‐specific differences in hospitalisation policies. We did not find statistically significant differences for mortality (very low quality), pneumonia (low quality), exacerbations, exercise capacity, quality of life and dyspnoea scores, adverse events and withdrawal (all moderate quality).

Authors' conclusions

We found little evidence to suggest that beclometasone is a safer or more effective treatment option for people with COPD when compared with placebo or when used in combination with LABA; when statistically significant differences were found, they mostly were not clinically meaningful or were based on data from only one study. The review was limited by an inability to obtain data from one study and likely publication bias for BDP versus placebo, and by the inclusion of one study only for BDP/LABA versus LABA. An ongoing study of BDP/LABA versus LABA may have a further impact on these conclusions.

Plain language summary

The effect of steroid inhalers containing the drug beclometasone for patients with COPD

Background

Chronic obstructive pulmonary disease (COPD; i.e. chronic bronchitis or emphysema or both, also called "smoker's lung disease") is a disease in which patients (predominantly smokers) experience breathlessness and produce a lot of phlegm or sputum. COPD is diagnosed by using international guidelines provided by the Global Initiative for Obstructive Lung Disease (GOLD).

One of the treatments that may be used to slow down worsening of this disease consists of steroid inhalers. These inhalers are known as preventer inhalers because they are taken daily to prevent symptoms. GOLD recommends that steroid inhalers are now to be used only in combination with inhaled LABA drugs (long‐acting beta₂‐agonists, e.g. formoterol). They are recommended for patients who have COPD with high risk of flare‐ups ("exacerbations").

Why do this review?

It is still unsure whether these steroid preventer inhalers, such as beclometasone inhalers, make a difference to patients with COPD.

Therefore we decided to do a systematic review of existing studies to look into the effects and side effects of beclometasone inhalers for people with COPD.

Which questions does this review try to answer?

Our study consisted of two parts: (A) Are beclometasone inhalers better than placebo? and (B) Is beclometasone in combination with LABA drugs in one inhaler (a beclometasone/formoterol combination inhaler) better than a LABA (formoterol) inhaler?

How did this review do this?

We searched all research papers of clinical trials on this topic and made a special effort to find unpublished trials.

We compared effects on breathing ability, death rates, how often pneumonias and flare‐ups happened, how often rescue inhalers had to be used, quality of life and side effects.

The evidence obtained is up to date to February 2013.

What were the results?

For (A) we found two studies, with a total of 298 study participants. For (B) we found one study, with 474 study participants, all with severe (stage 3) COPD.

For (A) we found no differences that could not be due to chance (not "statistically significant"). Therefore we found no evidence that beclometasone is better or worse than placebo for COPD. It is possible that this conclusion is not fully informed, however, as we were able to use only one trial. We await further statistics from another trial, and we suspect that many trials addressing (A) have gone unpublished in the past.

For (B) we found real differences in breathing capacity and rescue inhalers ("statistically significant"), but as the differences were small, they are unlikely to be noticeable for patients (not "clinically significant"). We also found a real increase in the average rate of severe flare‐ups of COPD requiring hospital admission when study participants were using steroid‐containing inhalers. However, the trial authors showed that these differences could have been caused by different hospital policies in the many countries that participated. For the other aspects that we compared, we found no differences in benefits or harms; any differences found were so small that they could have been due to chance. Further research is being done in this area, and findings of these studies may change our conclusions in the future.

Are there any criticisms of this review's results?

Our conclusions are limited by the small number of studies that were useful (only three), the poor/average quality of the evidence and the fact that most of these studies apply only to patients with severe but very stable COPD.

Summary of findings

Summary of findings for the main comparison. Beclometasone/LABA compared with LABA for COPD.

Beclometasone/LABA compared with LABA for COPD
Patient or population: participants with stable stage 3 COPD, smokers and ex‐smokers with a minimum pack‐year history of 20 Settings: 76 centres in 8 European countries (Bulgaria, France, Italy, Poland, Russia, Spain, Ukraine, United Kingdom) Intervention: beclometasone/formoterol Comparison: formoterol
Outcomes	Illustrative comparative risks* (95% CI)		Relative effect (95% CI)	No of participants (studies)	Quality of the evidence (GRADE)	Comments
	Assumed risk	Corresponding risk
	Formoterol	Beclometasone/Formoterol
Change in FEV1 Follow‐up: 48 weeks		Mean change in FEV1 in the intervention groups was 0.05 higher (0 to 0.1 higher)		465 (1 study)	⊕⊕⊕⊕ high
Mortality (all‐cause) (dichotomous Peto method) Follow‐up: 48 weeks	0 per 1000	0 per 1000 (0 to 0)	OR 7.48 (0.47 to 120)	474 (1 study)	⊕⊝⊝⊝ very low1,2,3
Pneumonia: participants with at least one (dichotomous Peto odds ratios) Follow‐up: 48 weeks	4 per 1000	16 per 1000 (3 to 76)	OR 3.88 (0.78 to 19.39)	474 (1 study)	⊕⊕⊝⊝ low2,3
Exacerbations: participants with at least one (dichotomous) Follow‐up: 48 weeks	283 per 1000	275 per 1000 (202 to 364)	OR 0.96 (0.64 to 1.45)	465 (1 study)	⊕⊕⊕⊝ moderate2
Change in quality of life: SGRQ Scale: 0 to 100 Follow‐up: 48 weeks		Mean change in quality of life: SGRQ in the intervention groups was 0.85 lower (3.32 lower to 1.62 higher)		465 (1 study)	⊕⊕⊕⊝ moderate2
Adverse events: candidiasis Follow‐up: 48 weeks			Not estimable	474 (1 study)	⊕⊕⊕⊝ moderate1
Withdrawal (all‐cause) Follow‐up: 48 weeks	143 per 1000	132 per 1000 (83 to 203)	OR 0.91 (0.54 to 1.53)	474 (1 study)	⊕⊕⊕⊝ moderate2
*The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (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; OR: Odds ratio.
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.

¹Indirectness of outcome. Unlikely to have been powered for this outcome. May be more appropriate to measure this outcome with e.g. a cohort study.
 ²Wide confidence intervals.
 ³Few events.

Summary of findings 2. Beclometasone compared with placebo for COPD.

Beclometasone compared with placebo for COPD
Patient or population: participants with stable stage 2 and 3 COPD (mainly FEV1 49 ± 12% predicted), ex‐smokers (majority), smokers and non‐smokers Settings: outpatient lung clinics in France (and additionally, for "withdrawals", the UK) Intervention: beclometasone Comparison: placebo
Outcomes	Illustrative comparative risks* (95% CI)		Relative effect (95% CI)	No of participants (studies)	Quality of the evidence (GRADE)	Comments
	Assumed risk	Corresponding risk
	Placebo	Beclometasone
Change in FEV1 —at 2 years Follow‐up: 2 years		Mean change in FEV1—at 2 years in the intervention groups was 0.03 higher (0.25 lower to 0.31 higher)		194 (1 study)	⊕⊝⊝⊝ very low1,2,3
Mortality (all‐cause) (dichotomous Peto method) Follow‐up: 2 years	53 per 1000	50 per 1000 (14 to 157)	OR 0.94 (0.26 to 3.34)	194 (1 study)	⊕⊝⊝⊝ very low2,3,4,5
Pneumonia: participants with at least one (dichotomous Peto odds ratios)			Not estimable	0 (0)
Exacerbations: participants with at least one (dichotomous)			Not estimable	0 (0)
Symptoms: change in dyspnoea scale (Fletcher Scale) Fletcher dyspnoea scale (1 to 5) Follow‐up: 2 years		Mean symptoms: Change in dyspnoea scale (Fletcher Scale) in the intervention groups was 0.05 higher (0.06 lower to 0.15 higher)		194 (1 study)	⊕⊕⊕⊝ moderate3
Adverse events: candidiasis Follow‐up: 2 years	21 per 1000	29 per 1000 (5 to 151)	OR 1.41 (0.24 to 8.31)	194 (1 study)	⊕⊝⊝⊝ very low2,3,5
Withdrawal (all‐cause) Follow‐up: 2 years	336 per 1000	402 per 1000 (295 to 520)	OR 1.33 (0.83 to 2.14)	292 (2 studies)	⊕⊕⊝⊝ low2,3
*The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (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; OR: Odds ratio.
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.

¹The Derenne 1995 study was assessed as at high risk of incomplete outcome data for FEV₁ (see the Derenne 1995 'Risk of bias' table).
 ²Wide confidence intervals (includes null effect).
 ³For the beclometasone versus placebo studies, we strongly suspected publication bias (see section "Potential biases in the review process").
 ⁴All‐cause mortality is a very objective outcome measure, and no significant difference was noted in participants lost to follow‐up through withdrawal.
 ⁵Indirectness of outcome, as the Derenne study was unlikely to be powered for comparing this outcome. A cohort study may be more appropriate.

Background

Description of the condition

Chronic obstructive pulmonary disease (COPD) is a condition with significant mortality and morbidity worldwide. The World Health Organization (WHO) reported that 63.6 million people suffered from the condition in 2004. It was the fourth leading cause of death, accounting for 5.1% of all deaths. Ninety per cent of deaths occurred in low‐income and middle‐income countries. Even so, in high‐income countries, it was still the fifth leading cause of mortality. As it is a chronic condition, it was the thirteenth biggest cause of disease burden worldwide, but it is projected to become the fifth by 2030 (WHO 2008).

According to the international guidelines provided by the Global Initiative for Obstructive Lung Disease (GOLD) and the guidelines of the American Thoracic Society/European Respiratory Society (ATS/ERS), a diagnosis of COPD is made in individuals with dyspnoea, chronic cough or sputum production and/or a history of risk factor exposure if their postbronchodilator forced expiratory lung volume in 1 second (FEV₁)/forced vital lung capacity (FVC) ratio is less than 0.70 (ATS/ERS 2004; GOLD 2010). Both guidelines classify COPD severity, according to postbronchodilator FEV₁, into stage 1 (mild); stage 2 (moderate); stage 3 (severe); and stage 4 (very severe), respectively, as FEV₁ ≥ 80% predicted; FEV₁ < 80% predicted; FEV₁ < 50% predicted; and FEV₁ < 30% predicted. This classification was subsequently adopted by the UK National Institute for Health and Clinical Excellence (NICE) in 2010 (NCGC 2010).

Although most intervention clinical trials are based around this spirometry‐based staging, FEV₁ alone is insufficient for prediction of disease severity (GOLD 2013). Hence, the GOLD 2013 guidance also takes into account individual patients' symptoms (using the COPD Assessment Test (CAT) or the modified British Medical Research Council questionnaire (mMRC)) and future risk of exacerbations (using either FEV₁ staging or the number of exacerbations in the last year, whichever denotes higher risk). Patients corresponding to stage 1 to 2 and/or with 0 to 1 exacerbations per year (low risk) will therefore belong to group A (CAT < 10 or mMRC grade 0 to 1; few symptoms) or group B (CAT ≥ 10 or mMRC ≥ 2; more symptoms). Patients deemed at high risk correspond to stage 3 to 4 and/or have ≥ 2 exacerbations per year, either with few symptoms (CAT < 10 or mMRC grade 0 to 1)—group C—or with more symptoms (CAT ≥ 10 or mMRC ≥ 2)—group D.

Description of the intervention

Beclometasone dipropionate is an inhaled corticosteroid (ICS) used in asthma and COPD. It was first introduced for asthma in 1972 (Brown 1972). In the UK and in many other countries, it is not licenced specifically for COPD, but because of the historical overlap between asthma and COPD, this practice has seldom been questioned. Other corticosteroids used include budesonide, fluticasone propionate and mometasone furoate. Inhaled corticosteroids are recommended as additional treatment to long‐acting beta₂‐agonists (LABAs) for stage 3 and 4 COPD patients with repeated exacerbations (ATS/ERS 2004; GOLD 2010; NCGC 2010). New guidance recommends inhaled corticosteroids combined with LABAs (or long‐acting anticholinergics alone instead) for group C patients; and ICS with LABAs and/or long‐acting anticholinergics, among other alternative options, for group D patients (GOLD 2013).

Available inhalers that combine ICS and LABA are fluticasone propionate and salmeterol (marketed as Seretide and Advair by GlaxoSmithKline), budesonide and formoterol fumarate (marketed as Symbicort by AstraZeneca), mometasone and formoterol (marketed as Dulera and Zenhale by Merck/MSD) and most recently beclometasone dipropionate and formoterol fumarate (marketed as Fostair and Foster by Chiesi).

How the intervention might work

Inhaled corticosteroids are thought to reduce local inflammation in the bronchial tree, thereby alleviating airflow obstruction. Beclometasone dipropionate itself is "a pro‐drug with weak glucocorticoid receptor binding affinity. It is extensively hydrolysed via esterase enzymes to the active metabolite beclometasone‐17‐monopropionate (B‐17‐MP), which has potent topical anti‐inflammatory activity" (MHRA 2006).

Why it is important to do this review

COPD places a high financial burden on healthcare budgets. In the UK, the annual per patient cost was estimated at GBP1639 in 2003 (Britton 2003). Because COPD is a chronic illness with frequent acute exacerbations requiring admission, a large proportion of this expense was due to secondary care costs (Britton 2003). It is therefore useful to put any treatment reviewed into the context of hospitalisations, as well as absolute treatment effect.

Treatment with ICS itself also represents a big cost for healthcare budgets. The now recommended (GOLD 2010; NCGC 2010) combination inhalers represent one of the biggest drug costs in the UK National Health Service (NHS), as their prescribing in primary care has increased in five years from GBP8 million to GBP30 million per quarter (NPC 2008).

Their effectiveness, however, is still debated (Anon. 2010; Lucas 2008; Suissa 2009; Welsh 2010).

Systematic reviews regarding the effectiveness and side effects of ICS in COPD have already been conducted (Agarwal 2010; Bradley‐Drummond 2008; Gartlehner 2006; Jones 2002; Loke 2010; Nannini 2007; Richy 2003; Rodrigo 2009; Selroos 2009; Spencer 2011; Welsh 2010; Yang 2007). Despite the fact that we know that different corticosteroids have different risks of adverse effects, debatably independent of their efficacy (Adams 2007; Clark 1997; Fabbri 1993; Kelly 2009; Lipworth 1999; Martin 2002; Wales 1999), none of the systematic reviews separated the different corticosteroids in their analysis. This issue was also raised by the last NICE COPD guideline development group (NCGC 2010).

Separate analyses of these commonly used corticosteroids are needed. They are expensive and questions have been raised about their effectiveness; therefore, it is worth considering beclometasone, one of the cheaper, less potent and already widely used ICS. The current review will therefore concentrate on beclometasone dipropionate and the evidence for its use versus placebo. As the current recommendation is to combine corticosteroids with LABAs, we will also review the comparison between combined beclometasone dipropionate/LABAs and LABAs alone. The new guidance recommending inhaled corticosteroids with long‐acting anticholinergics was published too late to be added as a third comparison.

As clinical decisions are based on effectiveness, risk of adverse effects and cost, this review will have implications for treatment choices. It is hoped that this review will stimulate future reviews that will look separately at the other ICS, so that these can then be synthesised as head‐to‐head comparisons.

Objectives

To determine the effectiveness and safety in COPD of inhaled beclometasone alone compared with placebo, and of inhaled beclometasone in combination with LABAs compared with LABAs alone.

Methods

Criteria for considering studies for this review

Types of studies

We included randomised controlled trials (RCTs) of parallel and cross‐over design.

We included only double‐blinded studies. For studies with ambiguous use of the term "blinding" or no mention of blinding at all, we assessed the risk of bias according to the specific outcome that it could have influenced. We excluded cluster‐randomised trials.

The length of follow‐up had to be at least 12 weeks.

Types of participants

Adult patients (> 35 years old) with an established diagnosis of stable COPD fulfilling the international guidelines, or equivalent guidelines. We assessed and discussed older studies that may not comply with current GOLD standards.

We excluded studies on COPD due to homozygous alpha‐1‐antitrypsin deficiency, as this is a rare genetic cause, and patients with this disorder may respond differently from those with COPD due to environmental risk factor exposure.

Patients could not have any other significant diseases that could affect measured outcomes, such as asthma or other respiratory diseases.

Types of interventions

1. Intervention: beclometasone administered by inhalation devices including metered dose inhalers, dry powder inhalers or spacer devices, but excluding nebulisers. We also considered co‐therapy with a long‐acting beta₂‐agonist (LABA) as long as it was used in both treatment and control arms of the trials.

2. Comparison: placebo.

We included studies with concurrent therapies and planned to investigate these by performing a subgroup analysis.

Types of outcome measures

Primary outcomes

1. Change in lung function (FEV₁, FEV₁/FVC).

2. Mortality (all‐cause and respiratory).

3. Pneumonia.

Secondary outcomes

1. Exercise capacity—e.g. six‐minute walk test (6MWT).

2. Number of participants experiencing one or more exacerbations of COPD (defined as worsening of the condition requiring hospitalisation or treated by oral steroids and/or antibiotics).

3. Number of exacerbations of COPD (defined as worsening of the condition requiring hospitalisation, treated by oral steroids and/or antibiotics).

4. Hospitalisations and length of stay.

5. Quality of life—St. George's Respiratory Questionnaire (SGRQ), Chronic Respiratory Disease Questionnaire (CRDQ). (We will exclude non–disease‐specific scales, such as the Short Form (36) Health Survey (SF‐36).)

6. Symptoms—e.g. change in Transitional Dyspnoea Index (TDI).

7. Use of rescue bronchodilators.

8. Other adverse events: oropharyngeal side effects (candidiasis, dysphonia), osteopoenia measures (bone fractures, bone density), diabetes, palpitations, tremor, skin bruising, plasma cortisol levels and cataracts.

9. Withdrawal.

Search methods for identification of studies

The search methods were formulated according to the template produced by the Cochrane Airways Group (CAG 2008). The Cochrane Airways Group's Trials Search Co‐ordinator (TSC) performed the search and supplied the results to the review author for the study selection process.

Electronic searches

We identified trials using the Cochrane Airways Group Specialised Register of trials (CAGR). This database is derived from systematic searches of bibliographic databases including the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, EMBASE, CINAHL, AMED and PsycINFO, and from handsearching of respiratory journals and meeting abstracts (see Appendix 1). We searched all records in the Specialised Register coded as 'COPD' using the following terms: 

(*steroid or steroid* or corticosteroid* or beclo* or beco* or asmabec or clenil or qvar or fostair).

We reviewed clinical guidelines and review articles for references by searching GOLD and NICE guidelines and conducting a search of the Centre for Reviews and Dissemination (CRD), Cochrane Database of Systematic Reviews (CDSR) and Turning Research Into Practice (TRIP) databases.

For grey literature, we searched the OpenGrey database, Zetoc and Web of Science for conference abstracts, and the World Health Organization International Clinical Trials Registry Platform (WHO ICTRP), clinicaltrials.gov, clinicaltrialsregister.eu, the National Research Register (NRR) archive and the International Federation of Pharmaceutical Manufacturers & Associations (IFPMA) Clinical Trials Portal for ongoing or completed studies.

We searched available pharmaceutical trial registers (AstraZeneca, Bayer, Bristol‐Myers Squibb, GlaxoSmithKline, Novartis, Roche, UCB).

We searched all databases from their inception to the present and imposed no restriction on language of publication.

Searching other resources

We reviewed reference lists of all primary studies for additional references. We contacted authors of identified trials and asked them to identify other published and unpublished studies. We also contacted manufacturers of any beclometasone inhalers past or present (Chiesi, UCB Pharma, 3M, Teva, GlaxoSmithKline and Merck/MSD) and obtained licensing information from the US Food and Drug Administration (FDA) through its website and from the UK Medicines and Healthcare products Regulatory Agency (MHRA) through a Freedom of Information request.

As this is a review of drug trials, and in most Western countries, these need both drug trial authorisation and ethics approval, we additionally contacted marketing authorisation bodies and/or central Ethics Committees for the European Union (EMA/EudraCT), the UK (MHRA and NRES), Armenia (SCDMT), Austria (AGES), Azerbaijan (DVAEM), Belarus (RCETH), Belgium (FAGG‐AFMPS), Bulgaria (BDA), Croatia (ALMP and MoH), Cyprus (PHS), Denmark (Lægemiddelstyrelsen), Estonia (SAM), Finland (FIMEA), Georgia (MoH), Germany (BfArM), Greece (EOF), Hungary (OGYI), Iceland (Visindasidanefnd, Lyfjastofnun), Ireland (IMB), Italy (AIFA), Kazakhstan (DARI), Kyrgyzstan (MoH), Latvia (ZVA), Lithuania (VVKT, LBEK), Luxemburg (DPM, CNER), Malta (Medicines Authority, MHEC), Moldova (AMED), Netherlands (CCMO), Norway (Legemiddelver), Poland (URPL), Portugal (INFARMED, CEIC), Romania (ANM, CNESCM), Russia (Roszdravnadzor, Rosminzdrav), Serbia (ALIMS), Slovakia (SUKL), Slovenia (JAZMP, NMEC), Spain (AEMPS), Sweden (MPA), Switzerland (Swissmedic), Tajikistan (MoH), Turkey (IEGM), Ukraine (DEC, MoZ), the USA (FDA), Uzbekistan (Uzpharm), China (SFDA), India (CDSCO), South Africa (MMC, NHREC), Mexico (MoH, INER, IMIC), New Zealand (MEDSAFE, HDEC) and Australia (TGA, NAA), and the following ethics committee organisations: Association of Research Ethics Committees (AREC), Forum for Ethical Review Committees in the Asian & Western Pacific Region (FERCAP), Forum for Ethics Committees in the Confederation of Independent States (FECCIS), Latin American Forum of Ethics Committees in Health Research (FLACEIS), Pan‐African Bioethics Initiative (PABIN), Council on Health Research for Development (COHRED) and International Conference on Harmonisation of Technical Requirements for Registration of Pharmaceuticals for Human Use (ICH).

We citation‐tracked identified studies to identify further studies.

Data collection and analysis

Selection of studies

One review author (DADC or NT) identified titles and abstracts that appeared to be relevant. We retrieved the full‐text trial reports, and two of us (DADC and MJ, or DADC and NT) independently assessed for inclusion all potential studies that we had identified as a result of the search strategy. We recorded excluded reviews that may appear to be relevant, along with an explanation for their exclusion. We resolved any disagreement through discussion or, if required, by consulting a third person, who is an expert in the field.

Data extraction and management

Two of us (DADC and MJ) extracted data from the selected studies using a data extraction form (initial outline: see Appendix 2), which was first piloted. When any doubt arose, we sought an expert opinion. One of us then entered data into Review Manager 5 (RevMan 2011), and a second review author checked this work. We obtained data missing from publication through correspondence with the study authors, using multiple media (electronic mail, letter, telephone), in all possible circumstances.

Assessment of risk of bias in included studies

Two of us (DADC and NT) independently assessed risk of bias for each study using the criteria and tools outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) (see Appendix 3). We resolved any disagreement by discussion or by involving a third assessor (MJ and, if necessary, our expert). We assessed the risk of bias according to the following domains.

1. Random sequence generation.

2. Allocation concealment.

3. Blinding of participants and personnel.

4. Blinding of outcome assessment.

5. Incomplete outcome data.

6. Selective outcome reporting.

7. Other bias.

We graded each potential source of bias as high, low or unclear risk of bias.

Measures of treatment effect

We analysed dichotomous data (such as exacerbations of COPD and pneumonia) using odds ratios (ORs) with 95% confidence intervals (CIs). We used the Mantel‐Haenszel method to combine estimates of ORs, except for rare events, for which the Peto method is more suitable.

We assessed continuous data (such as lung function, exercise capacity, quality of life and symptoms) using mean differences (MDs) (also known as "differences in means" or "weighted mean differences" (WMDs)) for absolute differences between mean values, or standardised mean difference (SMDs) for outcomes measured in different ways. When rate ratios were reported, we used the generic inverse variance (GIV) method.

We expressed time‐to‐event data (e.g. mortality) as a hazard ratio (HR), with a proportional hazards assumption.

Unit of analysis issues

We rigorously assessed cross‐over design studies on intervention and wash‐out periods, using expert input, as corticosteroids can have long‐lasting effects. Any cross‐over studies that were deemed not suitable were treated as parallel studies by including data from only the first period of the trial, before the cross‐over.

In studies with multiple treatment groups, we determined which intervention groups were relevant to this systematic review, and for which particular meta‐analysis. To avoid double‐counting, we divided the control group according to the number of interventions in the study.

We counted exacerbations as participants with one or more exacerbation(s); grouping together participants with one or multiple exacerbations prevented double‐counting of participants.

Dealing with missing data

When missing statistics could not be obtained from the trial authors, we used the reported CI or P value to calculate standard deviations (SDs) or standard errors (SEs).

We accounted for missing participants according to intention‐to‐treat (ITT) analysis, as well as the secondary outcome measure of "withdrawals".

We contacted trial authors to obtain missing data and clarify information on study design. Where quotes from correspondence have been used, permission from the author was obtained.

Assessment of heterogeneity

We used the I² statistic to assess statistical variation. If we identified substantial heterogeneity, we explored this by performing a prespecified subgroup analysis. 

Assessment of reporting biases

When we suspected reporting bias, we contacted study authors to ask them to provide missing outcome data. When this was not possible, and the missing data were thought to introduce serious bias, we explored the impact of including such studies in the overall assessment of results by conducting a sensitivity analysis. 

We assessed publication bias using a funnel plot and interpretation, as asymmetry in the funnel plot is not necessarily caused by publication bias. However, funnel plots are suitable only for assessment of ten or more studies.

Data synthesis

We created a 'Summary of findings' table by using the methods and recommendations described in Section 8.5 and Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), and by using GRADEpro software. We included the following outcomes.

1. Change in lung function (FEV₁, FEV₁/FVC).

2. Mortality (all‐cause and respiratory).

3. Pneumonia.

4. Exacerbations of COPD.

5. Adverse events.

6. Withdrawals.

Subgroup analysis and investigation of heterogeneity

We analysed the data using the following subgroups.

1. Dose of beclometasone (e.g. above and below 800 μg, as the lower‐strength beclometasone dipropionate products such as the now discontinued Becotide 200 were commonly prescribed up to this dose).

2. Delivery method of beclometasone (metered dose inhalers, dry powder inhalers or spacer devices).

3. Medium‐term (between three and six months) and long‐term (greater than six months) treatment periods.

4. Severity of condition at baseline according to GOLD criteria.

5. Prior use of ICS (dichotomised as yes/no).

6. Concurrent therapy: theophylline (dichotomised as yes/no).

Sensitivity analysis

We assessed the sensitivity to degree of bias of our primary outcomes by comparing overall results with those obtained exclusively from trials assessed as being at low risk of bias for the domains "randomisation" and "blinding". We compared the results from the fixed‐effect model with results from the random‐effects model.

Results

Description of studies

Results of the search

As recommended by the Preferred Reporting Items for Systematic Reviews and Meta‐Analyses (PRISMA) statement (Moher 2009), a study flow diagram has been included (Figure 1).

1.

PRISMA study flow diagram.

We identified 1243 records through database searching (CAGR, Zetoc, Web of Science, clincialtrials.gov, clinicaltrialsregister.eu, OpenGrey, WHO ICTRP, IFPMA, NRR archive, pharmaceutical trial registers, GOLD, NICE, CRD, CDSR, TRIP) and 511 through other sources (FDA; MHRA; personal communication; manufacturers/pharmaceutical companies; marketing authorisation/ethics committee organisations; using included trials to contact authors, review the reference lists and perform citation‐tracking for additional studies). (See Figure 1 and, for a detailed break‐down, Figure 2.) Based on title and abstract, 16 studies met our inclusion criteria. After the full‐text articles were assessed, four studies were deemed suitable for inclusion: Calverley 2010, Weir 1999, the unpublished Derenne 1995 and the ongoing Wedzicha (FORWARD) 2013. We obtained the unpublished Derenne full‐text study from the authors and requested additional data from the authors of the Weir study to include their data in the meta‐analysis (currently possible only for withdrawals). This was promised to us but is still pending.

2.

Detailed break‐down of results of the search strategy.

Included studies

Three studies were included (Calverley 2010; Derenne 1995; Weir 1999), the characteristics of which are described in detail in the Characteristics of included studies tables.

Calverley 2010

Calverley 2010 was a nearly year‐long (48 weeks) double‐blind randomised controlled trial that examined the effect of the new drug beclometasone/formoterol (BDP/FF) pMDI (pressurised metered dose inhaler) with a daily dose of 400/24 μg, against the effect of a formoterol (FF) DPI (dry powder inhaler) with a daily dose of 24 μg. (These are normal maximum dosages for BDP/FF and FF (GOLD 2010)). It investigated 476 (BDP/FF 237, FF 239) participants in 8 European countries, who had a mean age of 63.0 ± 9.5 years and were selected for COPD according to near‐accurate GOLD guidelines (a 30‐minute postbronchodilator (post‐BD) change in FEV₁ of less than 12% was required, although GOLD standards specify 10 to 15 minutes post‐BD). This was a study of participants with stage 3 (severe) COPD (a post‐BD FEV₁ between 30% and 50% of the predicted normal). Participants were required to have been stable for a two‐month run‐in period. The trial required a pack‐year history of at least 20 years for inclusion, with two‐thirds of participants being ex‐smokers. The outcomes of interest measured were pulmonary function tests (FEV₁); mean rate of COPD exacerbations; Modified Medical Research Council dyspnoea score questionnaire; St. George’s Respiratory Questionnaire (CRDQ) to gauge quality of life; exercise capacity using the six‐minute walking test (6MWT); a body mass index, airflow obstruction, dyspnoea and exercise capacity index (BODE); use of rescue bronchodilator and several adverse events. Withdrawal and mortality were deduced by the review authors (DADC, MJ) from the data, using the numbers quoted in the text and in the tables.

The trial contained a third treatment arm (comparing both BDP/FF and FF in separate inhalers with budesonide/formoterol (242 participants randomly assigned)), but this comparison was not relevant for this review.

Derenne 1995

The Derenne 1995 study previously appears in the literature only as a conference abstract but as part of another meta‐analysis (van Grunsven 1999), which was performed to look summatively at several different ICS. The original full‐text article, however, has not been published. Several of the Derenne 1995 authors are co‐authors in that meta‐analysis, which implies that they worked closely with the latter group to lend them their data. However, it is not possible to separate out the Derenne 1995 data retrospectively from data from the other studies, all of which address different ICS than BDP. Although we contacted the van Grunsven 1999 authors, it was also not possible to obtain the original Derenne data from them. As stated above, however, we were successful in obtaining two different versions of the unpublished full‐text article; one from Derenne 1995 co‐author T. Similowski (without figures, but with additional appendices) (Personal communication by email, 15/05/2012), and one as a chapter in the thesis of P.M. van Grunsven, available online (with figures, but without appendices; minor improvements in the abstract), also found by T. Similowski (Personal communication by email, 4/12/12).

Derenne 1995 investigated beclometasone versus placebo. This was a 2‐year‐long study based in France that compared beclometasone dipropionate (Becotide) 1500 μg daily with placebo. This is a high‐dose study: 1500 μg is considerably more than the maximum 1000 μg per day recommended at the time, received through equivalent chlorofluorocarbon (CFC) inhalers (BTS 1997), which may be substantially different from currently used hydrofluoroalkane (HFA) beclometasone inhalers (Leach 1998). A total of 100 participants using BDP were randomly assigned versus 94 participants receiving placebo, with average age around 63 years (BDP 62 (SD 7); placebo 63 (SD 8)). It is not clear from the text whether concomitant drug use (of theophyllines, of anticholinergics, etc.) was ceased at the start of the trial. The diagnostic criteria used included the ATS 1987 guidelines (of a clinical diagnosis of COPD based on history) and staging of pre‐bronchodilator FEV₁ that was 30% to 60% of predicted (this compares with modern GOLD stage 3 COPD of 30% to 50% predicted and the remainder (50% to 60% predicted) falling within GOLD stage 2). Participants had to have 10‐minute postbronchodilator reversibility less than 15% of the predicted FEV₁. This trial included smokers, ex‐smokers and non‐smokers; most participants were ex‐smokers. Outcomes of interest were post‐BD FEV₁; exacerbations, defined as "prescribed courses of antibiotics or oral corticosteroids"; Fletcher Dyspnoea Scale scores (Fletcher 1964); hospitalisation and duration; adverse events; and withdrawal and mortality (both deduced by the review authors (DADC, MJ)).

Weir 1999

The Weir 1999 study compared beclometasone only versus placebo. It was a 2‐year‐long double‐blind parallel randomised placebo‐controlled trial based in the UK that investigated the effect of a daily dose of 1500 μg of BDP if participants' weight  was below 50 kg, and 2000 μg if weight was over 50 kg. The control was a placebo inhaler, with an equivalent weight‐based number of puffs. Participants who were taking oral theophyllines before the study maintained the same dose throughout the study. The number of participants randomly assigned was 98 (BDP n = 49, placebo n = 49), and they had an average age of 66 years. The diagnostic criteria included a clinical diagnosis of COPD, adult‐onset airflow obstruction with FEV₁ < 70% predicted and FEV₁/FVC ratio < 65%. Patients were excluded if they had clinically significant bronchodilator reversibility or a history of significant improvement with steroid treatment; or if steroid treatment was clinically indicated. Other criteria for exclusion included prescribed use of any form of corticosteroid therapy for longer than three months in the previous year or prescribed use of any form of steroid therapy during the 4‐week run‐in period. This trial included smokers and ex‐smokers, but most participants were ex‐smokers. The outcomes of interest included change in post‐BD FEV₁, rate of exacerbations (no description of what was defined as an exacerbation was provided), change in BDI (Baseline Dyspnoea Index) or CRDQ (in a subgroup of participants, but data declared as not reported in this publication) and withdrawal.

Excluded studies

A detailed description of excluded studies is provided in the Characteristics of excluded studies tables.

One study had inadequate inclusion criteria to exclude asthmatic patients (Boothman‐Burrell 1997), four studies were excluded because they were not randomised trials (Dinc 2001; Miravitlles 2002; Struijs 1997; van Schayck 1995), two were not double‐blinded (Ouyang 1998 after translation, Shmelev 2006), three had treatment periods that were too short (Thompson 1992; Weir 1990; Weir 1993) and one did not address the appropriate research question (Tzani 2011). Last, one study was excluded because of insufficient data (John 2005); expert opinion was that the wash‐out period in this cross‐over trial was insufficient, and therefore, as per protocol, we would try to include it as a parallel trial, using only data from the first treatment period. However, when the trial authors were contacted, they were unable to provide data from the first treatment period only.

Ongoing studies

One ongoing study was identified as potentially relevant (Wedzicha (FORWARD) 2013) (see Characteristics of ongoing studies). It was a 48‐week double‐blind trial with 1119 participants in 5 European countries of BDP/FF 100 µg/6 µg (daily dose not known yet) versus FF 12 µg (cf. the included Calverley 2010). Participants had to have severe COPD and had to be older than 40 years of age. Outcomes of potential interest would include exacerbation rate; change in FEV₁; further lung measurements; SQRQ; and use of rescue inhalers.

The study will be known as "FORWARD" (Foster 48‐Week Trial to Reduce Exacerbations in COPD); investigators were expected to report at "the ATS in May" 2012, and the article was to be published later (Personal communication by email, 19/03/13).

Studies awaiting classification

One study is awaiting classification (Vengerov 1998), as only the abstract is currently available, and it does not contain enough information regarding trial design, blinding, inclusion criteria and minimum age of participants to allow the study to be assessed for inclusion (see Characteristics of studies awaiting classification). It is a 5‐year "randomised prospective trial" of 89 non‐smoking metal workers in Ukraine with COPD due to industrial pollution, with an FEV₁ of 46% to 70% predicted. The trial investigated a daily dose of 750 to 1250 μg beclometasone dipropionate versus observation, and potential outcomes of interest were change in FEV₁; number of exacerbations; length of hospitalisations; and symptom score. We tracked down the trial author, who now works in a different country and has promised to get the Russian full‐text article to us (Personal communication by email, 12/11/12) but has not yet done so. This may also be in investigation into a different form of COPD—a form caused by industrial mining.

Risk of bias in included studies

A detailed description of the risk of bias assessments per study is presented in the Characteristics of included studies section and is graphically summarised below (Figure 3 and Figure 4).

3.

Risk of bias graph: review authors' judgements about all risk of bias items presented as percentages across all included studies.

4.

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

Allocation

In Calverley 2010, methods to reduce risk of selection bias were adequately described. The random sequence was generated by a centralised computerised system and was used to allocate participants for concealment of allocation.

Derenne 1995 and Weir 1999 provided insufficient information on randomisation, with the former having inadequate information regarding rigorous methods to conceal allocation, and the authors of the latter providing evidence of central allocation and further allocation concealment in a personal communication.

Blinding

In both Calverley 2010 and Weir 1999, blinding of both participants and personnel and blinding during the measurements were adequate.

Derenne 1995 provided insufficient detail to allow conclusions to be drawn on blinding adequacy, but study drugs were "supplied" to the personnel, implying the possibility that adequate blinding of personnel and participants was maintained.

Incomplete outcome data

Calverley 2010 was deemed at low risk of attrition bias. Missing information was dealt with in an ITT analysis using the last observation carried forward (LOCF) method.

Derenne 1995 and especially Weir 1999 suffered from high withdrawal rates. Derenne 1995 warns that because of the reduced number of measurements used in the multivariate analysis, FEV₁ results should be interpreted with caution. Although risk of bias due to withdrawal of the most severely affected participants in Weir 1999 was minimised (because the numbers of withdrawals from each arm was balanced and, if the risk of bias was present, it would underestimate the effect of BDP treatment), Weir did not perform a conventional ITT analysis but analysed only participants with at least 12 months' follow‐up (i.e. only participants who completed at least half the length of the study).

Selective reporting

Calverley 2010 referred to a protocol‐like trial record in the full text and described only minor differences from all versions of this trial record. Derenne 1995 was compared with an earlier abstract publication and was deemed at low risk of reporting bias.

Weir 1999 did not report the final numbers used in each treatment arm of their analysis (only participants with at least 12 months' follow‐up were analysed) and did not report the Guyatt questionnaire data, as recording of these measures was compromised by lack of clinical staff during a period of the trial.

Other potential sources of bias

Calverley 2010 was funded by Chiesi. This was declared in the paper, as was conflict of interest information.

Derenne 1995 was funded by GlaxoWellcome France, which was declared. As it was an original manuscript, risk of publication bias was minimal.

Weir 1999, however, declared neither their funding information (GlaxoWellcome was involved in randomisation, provision of the drugs and performance of the analysis) nor conflicts of interest. Authors also "... had great difficulty in getting the paper published; it was turned down by many journals and was published as an extended conference proceeding where the requirements were for a cut‐down paper" (Personal communication by email, P.S. Burge, 20/12/12). This would explain the lack of many methodological details in the full text.

Effects of interventions

See: Table 1; Table 2

Because of incomplete reporting in Weir and the unfinished Wedzicha study, only the Calverley and Derenne studies were included quantitatively for most outcomes, and Weir was included narratively in the review (except for withdrawals). As Calverley addresses a different research question from that pursued by Derenne and Weir, the only meta‐analysis was performed on these latter two, and only for the withdrawals outcome. (For a full discussion on whether to combine these research questions into a meta‐analysis, see Overall completeness and applicability of evidence. For a full discussion of why the meta‐analysis could be done only for withdrawals, see this outcome under Effects of interventions.)

As only one trial per review arm was analysed quantitatively, we did not carry out any of the planned subgroup analyses or sensitivity analyses.

The readers are reminded that current international guidelines do not recommend the use of beclometasone alone (or any ICS) without LABA in COPD (ATS/ERS 2004; GOLD 2013).

Primary outcomes

Difference in lung function

Beclometasone versus placebo

Using the absolute value of change in lung function, at 2 years, the Derenne 1995 study (n = 194 participants) reported a statistically non‐significant change in (postbronchodilator) FEV₁ of 0.03 litres (95% CI ‐0.25 to 0.31, P = 0.83] for BDP compared with placebo.

At only 1 year, Derenne showed a statistically non‐significant (ns) change of ‐0.07 (95% CI ‐0.35 to 0.21, P = 0.63] for BDP compared with placebo.

These two results are shown in Analysis 1.1, where 1‐year and 2‐year results have not been combined into an overall effect, as they are measurements taken at different time points in the same participants.

1.1. Analysis.

Comparison 1 Beclometasone versus placebo, Outcome 1 Change in FEV₁.

At 2 years, the Weir 1999 study reported a statistically non‐significant slower mean rate decline of FEV₁ in BDP compared with placebo with 95% CI ‐0.080 to +0.008 L/y. This is derived from its unconventional intention‐to‐treat analysis of only participants who completed a full year of the study (n = 78). No point estimate was given.

Beclometasone/LABA versus LABA

At 48 weeks, the Calverley 2010 (n = 465) study reported a statistically significant increase in FEV₁ of 0.051 L (95% CI 0.001 to 0.102, P = 0.046) for BDP/LABA versus LABA, which is unlikely to be clinically significant (a change of 0.200 L; Cazzola 2008).

None of the trials reported FEV₁/FVC ratio, so these data are not included so far in this review.

Mortality

Information was insufficient to calculate HRs for all‐cause or respiratory mortality; this method is preferred to the use of odds ratios (Higgins 2011, Chapter 9.2.6). Therefore, we had to use odds ratios.

Beclometasone versus placebo

No evidence suggests that all‐cause mortality is altered further by BDP compared with placebo; Derenne 1995 (n = 194) showed a non‐significant difference (Peto OR 0.94, 95% CI 0.26 to 3.34, P = 0.92).

No evidence indicates that respiratory mortality was altered further by BDP compared with placebo. Derenne 1995 (n = 194) reported a non‐significant Peto OR of 7.03 (95% CI 0.44 to 113.35, P = 0.17; Analysis 1.3).

1.3. Analysis.

Comparison 1 Beclometasone versus placebo, Outcome 3 Exacerbations: mean rate (rate ratio).

Weir 1999 did not document any mortality data.

Beclometasone/LABA versus LABA

No evidence suggests that all‐cause mortality is altered further by BDP/FF compared with FF, with Calverley 2010 (n = 474) showing a non‐significant Peto OR of 7.48 (95% CI 0.47 to 120.00, P = 0.16).

Calverley 2010 reported zero events of respiratory mortality in either treatment arm; odds ratios cannot be calculated for zero events.

Pneumonia

Beclometasone versus placebo

None of the mono‐inhaler trials reported pneumonia events.

Beclometasone/LABA versus LABA

Based on the assumption that the absolute values for self‐reported pneumonias reported in Calverley 2010 (n = 474) pertained to different participants each time, we analysed pneumonia as dichotomous odds ratios using the Peto method. No evidence was found of any difference between BDP/LABA and LABA in terms of the risk of pneumonia (Peto OR 3.88, 95% CI 0.78 to 19.39, P = 0.10).

Secondary outcomes

Exercise capacity

Only Calverley 2010 (n = 465) included the six‐minute walking test in its outcomes; investigators reported no evidence of any difference between BDP/LABA and LABA (MD 6.00 metres, 95% CI ‐8.92 to 20.92, P = 0.43).

Number of participants with exacerbations

Only Calverley 2010 (n = 465) reported exacerbations as "number of patients with at least one exacerbation". No evidence was found of any difference between BDP/LABA and LABA (OR 0.96, 95% CI 0.64 to 1.45, P = 0.86).

Number of exacerbations

Beclometasone versus placebo

Using the logistic regression analysis rate ratio reported in the paper for steroid courses, Derenne 1995 (n = 194) provided no evidence of a difference in exacerbations for BDP vs placebo (RR 0.80, 95% CI 0.23 to 2.80, P = 0.73). For exacerbations, the study states the numbers of steroid courses and antibiotic courses separately. We chose to use the number of oral steroid courses as a more accurate reflection of an exacerbation than the number of antibiotic courses.

Data were insufficient to allow meta‐analysis in Weir 1999, but investigators reported a “non‐significant” lower rate of exacerbations per year in the BDP group (0.36 exacerbations/y (SE 0.09)) than in the placebo (0.57 (SE 0.13)).

Beclometasone/LABA versus LABA

When mean rates of exacerbations per year per participant reported in Calverley 2010 (n = 465) were used, no evidence was found of a statistically significant difference for BDP/LABA compared with LABA (RR 0.97, 95% CI 0.69 to 1.37, P = 0.88).

Hospitalisations and length

Beclometasone versus placebo

In Derenne 1995 (n = 194), the number of (presumably all‐cause) hospitalisations was reported in absolute values, but rate ratios could not be calculated without data on the length of study treatment exposure of each arm.

For duration of hospital stay, rate ratios could not be calculated, but the authors reported, "After correction for the total number of days of treatment (56,949 in the beclomethasone and 55,149 in the placebo group), this difference was not found to be significant (Z‐score = 0.93, Wilcoxon rank test)." Because data are skewed, they are not meta‐analysable.

Weir 1999 did not report on hospitalisations.

Beclometasone/LABA versus LABA

Hospitalisations that were due to exacerbations were reported in Calverley 2010 (n = 465) both as "patients with at least one exacerbations leading to hospitalisation", with a non‐significant difference (OR 1.67, 85% CI 0.68 to 4.11, P = 0.26), and as "mean rate of exacerbations leading to hospitalisation", with a significantly increased rate ratio for BDP/LABA from 0.040 per year on LABA to 0.074 per year on combination treatment (RR 1.84, 95% CI 1.17 to 2.90, P = 0.008). The study authors performed a post hoc analysis to account for differences in hospitalisation between countries; however, we did not use this analysis (see Quality of the evidence).

Quality of life

Calverley 2010 (n = 465) reported a bigger decrease in SGRQ (a high score is worse) for BDP/LABA, with a mean difference of ‐0.85 (95% CI ‐3.32 to 1.62, P = 0.50). This finding was neither statistically nor clinically significant (i.e. a change of > 4 SGRQ units).

Symptoms

Beclometasone versus placebo

Derenne 1995 used the Fletcher Dyspnoea Scale (Fletcher 1964) (a high score is worse) and reported no evidence of a difference between BDP and placebo (MD 0.05, 95% CI ‐0.06 to 0.15, P = 0.40). For this calculation, we had to impute the final values in both arms, as only baseline values and an estimate of the yearly difference (with an SE and P value) were reported.

The Fletcher Dyspnoea Scale (scale from 1 to 5) is very similar to the now more commonly used modified Medical Research Council dyspnoea questionnaire (scale from 0 to 4) (also used in Calverley 2010—see below).

Despite small improvements, Weir 1999 reported “no significant effect of active treatment on the Baseline Dyspnoea Index over the study period”.

Beclometasone/LABA versus LABA

Calverley 2010 (n = 465) used the modified Medical Research Council dyspnoea questionnaire (Mahler 1988) (a high score is worse). They reported no evidence of a difference between BDP/LABA and LABA (MD ‐0.12, 95% CI ‐0.26 to 0.02, P = 0.08).

The Body Mass Index, airflow Obstruction, Dyspnoea and Exercise capacity (BODE) Index (Celli 2004) was also used in Calverley 2010. No evidence was found of any difference in the BODE index (MD ‐0.17, 95% CI ‐0.40 to 0.06, P = 0.14).

Use of rescue bronchodilator

In Calverley 2010, a statistically significantly difference was reported, with participants in the BDP/LABA group self‐reporting more days without rescue bronchodilator compared with the control group (MD 7.05, 95% CI 0.84 to 13.26, P = 0.03).

Other adverse events

Beclometasone versus placebo

For oral candidiasis, Derenne 1995 (n = 194) showed no significant difference (Peto OR 1.41, 95% CI 0.24 to 8.31, P = 0.70).

For dysphonia, Derenne 1995 (n = 194) had a higher odds ratio for BDP than for control; this bordered on statistical significance (Peto OR 7.18, 95% CI 0.99 to 51.78, P = 0.05).

Third, for bone fractures, Derenne 1995 (n = 194) showed no significant difference (Peto OR 7.03, 95% CI 0.44 to 113.35, P = 0.17).

Weir 1999 makes no mention of other adverse events.

Beclometasone/LABA versus LABA

For oral candidiasis, dysphonia and bone fractures, Calverley 2010 (n = 474) had no events in either arm, which means that the OR is mathematically not estimable for any of these outcomes.

Events picked up by QTc interval evaluations and Holter cardiac monitoring are reported narratively only as “rare” in the Results section, and as “none” in the Discussion. For serum cortisol levels, changes from baseline were reported narratively as non‐significant in any group (section “Safety Evaluation”). The plasma glucose levels also were not reported in the Calverley study.

Withdrawal

Beclometasone versus placebo

For most outcomes, we were not able to use the Weir 1999 results in our meta‐analysis because investigators did not perform an intention‐to‐treat analysis. This problem does not have an impact on the number of withdrawals, however, which is based on the number of participants allocated and randomly assigned at the beginning of the study. Hence, for withdrawals only, we were able to combine Weir 1999 meta‐analytically with the other beclometasone mono‐inhaler study.

All‐cause withdrawal

For withdrawal due to any reason, combining the two BDP versus placebo studies (Derenne 1995; Weir 1999; n = 292) revealed no difference (Peto OR 1.33, 95% CI 0.83 to 2.14, P = 0.23; I² = 0%; Analysis 1.6).

1.6. Analysis.

Comparison 1 Beclometasone versus placebo, Outcome 6 Withdrawal.

Adverse event withdrawal

No significant difference was found in the rate of non‐completion due to adverse events for BDP (OR 1.06, 95% CI 0.52 to 2.19, P = 0.87; Derenne 1995; n = 194).

Respiratory withdrawal

Two studies (Derenne 1995; Weir 1999; n = 292) had withdrawal also coded as due to "ineffectiveness of treatment". The meta‐analysis showed no significant difference (Peto OR 1.55, 95% CI 0.60 to 4.04, P = 0.36; I² = 0%).

Beclometasone/LABA versus LABA

All‐cause withdrawal

Calverley 2010 (n = 474) showed no evidence that BDP/LABA altered the odds of withdrawal for any reason compared with LABA (Peto OR 0.91, 95% CI 0.54 to 1.53, P = 0.72).

Adverse event withdrawal

No evidence was found to show that BDP/LABA altered the rates of non‐completion due to adverse events (Peto OR 1.82, 95% CI 0.63 to 5.25, P = 0.27; Calverley 2010; n = 474).

Discussion

Summary of main results

The main results are summarised in two 'Summary of findings' tables: one for beclometasone/LABA versus LABA (Table 1) and one for beclometasone versus placebo (Table 2).

Beclometasone versus placebo

For beclometasone mono‐inhalers compared with placebo, no statistically significance differences were found in lung function, all‐cause mortality, respiratory mortality, number of exacerbations, number of hospitalisations, symptom scores, adverse events, all‐cause withdrawal and adverse event withdrawal. No data were available on pneumonia, quality of life scales or use of rescue bronchodilators.

The quality of the evidence was graded as very low for the outcomes of lung function, pneumonia and all‐cause withdrawal, low for the adverse event candidiasis and moderate for the symptom scores (see Table 2 for GRADE reasons).

Participants were mainly GOLD stage 2 and 3 COPD sufferers (post‐bronchodilator predicted FEV₁ around 49% (± 12%) in Derenne 1995 (n = 194) and around 43% (± 14%) in Weir 1999 (n = 98)) whose condition had been stable for the previous 3 months. They had on average a 39‐pack‐year history, and most were smokers or ex‐smokers; only 21 participants were never‐smokers.

Most of these studies were set in outpatient clinics in France; some took place in the UK.

Beclometasone/LABA versus LABA

For beclometasone inhalers combined with LABA (e.g. BDP/FF) compared with inhalers with LABA alone, statistically significant improvements were noted in lung function measurements and self‐reported days without rescue inhalers, both of which are clinically insignificant. A statistically significant increase was seen in the rate of exacerbations leading to hospitalisation for the combination inhaler, but this might be a false‐positive result. No statistically significant changes were noted in all‐cause mortality, pneumonia, exercise capacity, number of participants with exacerbations, rate of exacerbations, quality of life scores, symptom scores, all‐cause withdrawal and adverse event withdrawal. No difference was found in respiratory mortality, and no data were available on all‐cause hospitalisations.

The quality of this evidence was graded as high for lung function and as moderate for exacerbations and most other outcomes, but as low and very low for pneumonia and mortality, respectively (see Table 1 for GRADE reasons).

Participants were stage 3 COPD sufferers (postbronchodilator predicted FEV₁ was around 45% at baseline) who had been stable for 3 months (including the 4‐week run‐in period). They had a minimum pack‐year history of 20 (participant average 36 pack‐years) and two‐thirds were ex‐smokers.

This study took place in 8 European countries.

Overall completeness and applicability of evidence

Four randomised controlled trials were identified that were relevant to only one of the arms of the review question: BDP versus placebo (2 studies: Derenne 1995; Weir 1999) and BDP/LABA versus LABA (1 included study (Calverley 2010) and 1 ongoing study (Wedzicha (FORWARD) 2013)).

For a complete picture of the effects of inhaled beclometasone, it was important that the BDP versus placebo arm was included. The external applicability of this arm, however, is limited by current international guideline recommendations of using only BDP/LABA inhalers (see Description of the intervention).

After consulting with the Cochrane Airways Group, we chose not to combine these two review arms meta‐analytically for several reasons.

1. The combination inhalers (BDP/LABA) use extra‐fine particles of BDP, which is not the case with the mono‐inhalers used in the other review arm (Qvar is a mono‐inhaler with extra‐fine particles, but it is not used in studies in this review). Therefore, the doses of beclometasone used in the two arms were not equivalent, with extra‐fine particles being more potent. It is thought that doubling the dose of extra‐fine particles would make the dosing in the two arms roughly equivalent.

2. Between the two arms, only data at the same time point are provided for one outcome (FEV₁ at 1 year). As lung function does not follow a linear relationship of improvement on ICS treatment over time (Figure 2E, TORCH 2007), it is therefore imprudent to combine outcomes from different time points.

3. For all outcomes, we do not know how the addition of formoterol fumarate in the BDP/LABA treatment arms affected the effects of the BDP component compared with the mono‐inhaler BDP in the other review arm. Combination therapy seems to behave better than ICS monotherapy (TORCH 2007), and LABA has been shown to have a beneficial effect on its own (TORCH 2007).

4. In the BDP/LABA versus LABA arm of the review, BDP/LABA contains FF extra‐fine metered dose inhaler particles in the treatment arm (Foster) but FF dry powder metered dose inhaler particles in the comparison arm (Oxis). Again, this may reflect a different effective treatment dose.

BDP/LABA versus LABA

The included BDP/LABA versus LABA study (Calverley 2010) addressed most of the review’s outcomes, only lacking the outcomes hospitalisation and length of stay, and some of the projected adverse events (candidiasis—very important to patients, osteopoenia measures, tremor, skin bruising and cataracts). However, the study was too short to allow assessment of mortality. Observational studies could be used to assess these questions, but only randomised controlled trials were included in this review.

The participants assessed in this arm were mainly stage 3 COPD sufferers, although their conditions were well controlled because of the long run‐in period.

The dose of BDP/FF used in this arm was the normal recommended maximum dose (400/24 μg) (GOLD 2010).

The formoterol inhaler used as the comparator was delivered in a dry powder inhaler (DPI) device, whereas the formoterol in the BDP/FF arm was delivered through a metered dose inhaler (MDI) device. DPIs and MDIs behave differently in vitro (Longest 2012) and may have different effectiveness in a real‐world setting (Price 2011), although systematic reviews of RCTs have found no real difference between inhaler types (Brocklebank 2001a; Brocklebank 2001b; Dolovich 2005). Kemp 2010 suggested that the difference between real‐life and RCT findings may be selection bias in RCT participant demographics or the extensive training in inhaler technique received by RCT participants. Furthermore, with all of the evidence cited above, no trials compare DPIs with extra‐fine particle MDIs (such as the one used in the BDP/FF arm of Calverley 2010), which provide better drug delivery than normal MDIs (Ivancsó 2013).

Despite the discussion on whether the dose‐delivery curve is different for the two formoterol drugs used in Calverley 2010, the study does enable clinicians to assess whether a BDP/FF MDI is worth considering over available FF DPI drugs in a real‐life clinical setting. Hence this review arm remains externally applicable for the reader.

The other BDP/LABA versus LABA study, highlighted for future inclusion (Wedzicha (FORWARD) 2013), compares an FF MDI device versus a BDP/FF MDI. This may have been done to avoid the issue of how DPI beta‐agonist doses compare with MDI doses. Some trials indicate a "twofold to threefold greater potency" for DPIs of the same brand compared with MDIs, but other trials suggest that some brands of DPI (e.g. Spiros) could change this relation to approximate equipotency (Dolovich 2005). This difference between our two BDP/LABA versus LABA studies in their LABA comparator arms will have to be addressed when the decision is made whether to synthesise these studies in the next update.

BDP versus placebo

The BDP versus placebo arm of the review contains older studies and less well‐addressed outcomes. These studies did not report on pneumonia, exercise capacity and quality of life scores. The Weir 1999 study additionally did not report on mortality and adverse outcomes.

Participants in the Weir 1999 study were also mainly stage 3 COPD sufferers, although with a wider normal distribution (the inclusion criterion was < 70% FEV₁; the baseline characteristics were FEV₁ predicted of 41.4% (SE 16) and 39.7% (SE 16) for placebo and BDP, respectively). Interpretation of the staging of the Derenne 1995 participants is more complex as was their inclusion criterion (pre‐bronchodilator, likely) of FEV₁ 30% to 60% of predicted. Modern staging, however, is done postbronchodilator. Expert opinion was that prebronchodilation or postbronchodilation status was unlikely to affect the staging significantly, and that therefore we could regard these participants as mainly GOLD stage 3 (30% to 50% predicted), with the remainder (50% to 60%) in GOLD stage 2.

The doses used in this arm were relatively high, reaching 1500 μg—more than the then‐recommended maximum of 1000 μg (BTS 1997). The inhalers were CFC‐propellant inhalers, unlike the HFA inhalers used now. The dosing relationship of CFC inhalers compared with HFA inhalers is being debated (Kunka 2000; Leach 1998).

Quality of the evidence

A Grading of Recommendations Assessment, Development and Evaluation (GRADE) rating has been given to each outcome reported per review question arm, along with an explanation for the grading, in the 'Summary of findings' tables (Table 1; Table 2).

Overall, the identified body of evidence does not allow a robust conclusion regarding the review’s objectives. Only three studies were included, with a total of 768 participants and with 175 participants not completing the trials.

Weir 1999

The Weir 1999 study especially suffered a high dropout rate, retaining only 60% of its participants after the full two years. This highlights the difficulty involved in answering the question of steroid effectiveness in COPD. The gold standard comparison for any medication is placebo control. Whereas the Calverley 2010 control group was being treated with formoterol (which has some beneficial effects in itself), participants in the control group of Weir 1999 were taking no medication (except symptomatic relief medication, with a few participants taking theophylline). This is not sustainable in a chronic, progressively worsening condition over a long period of time, and it may explain the high dropout rate (no data were provided on whether the dropout rate was higher in the placebo or the treatment group, but participants who withdrew had "significantly worse lung function").

This was compounded by the lack of ITT analysis in the Weir 1999 study, along with a limited description of its methods, leading to a bias assessment that was mainly graded as "unclear".

Derenne 1995

The Derenne 1995 study had some methodological queries that could not be resolved when the remaining co‐authors were contacted because of the age of the study. First, we were not sure whether co‐pharmacy with anticholinergics, beta₂‐agonists, theophylline, mucolytics and almitrine (a respiratory stimulant) was present throughout the trial. Participants were allowed to take these during the pretrial assessment, but it is not specified whether they were discontinued at the start of the trial. The co‐authors have not been able to contact Derenne since 1999. As for the two co‐authors who were contactable, Professor van Weel said, “… I have to rely totally on my memory for this. And according to me, after the inclusion into the study, everyone was placed on the per protocol trial medication with the per protocol rescue medication” [translated, email 18/2/13], whereas Dr Similowski said, “Unfortunately, I cannot tell you more than what is in the manuscript. Logic has it that the treatments were continued, but I cannot be sure. I do not see any means to get the information. Most sorry” [email 18/2/13]. The table of baseline characteristics mentioned the percentage of participants receiving each concomitant drug under the subheading "Concomitant drugs (continuous use)". It is again unclear whether "continuous use" meant that the listed drugs were included in the table only if the participants had previously been receiving continuous therapy for a while, or whether they were continued throughout the trial.

Regarding FEV₁, the actual values and confidence intervals used in the analysis were obtained through manual measurement of the published figure, as these postbronchodilator values were not numerically reported in the paper, which devotes more description to the now devalued pre‐bronchodilator spirometry measurements.

Also, the study itself warns that the post‐BD FEV₁ measurements must be interpreted with caution because of the missing values in the multivariate analysis. Hence, the GRADE quality assessment for this outcome was downgraded.

For the exacerbation outcome, Derenne 1995 used a system of respiratory clinic appointments in screening for exacerbation problems. After participants were seen in the clinic, a decision would be made whether their current respiratory problem needed treatment with antibiotics, steroids or both. This almost walk‐in system might be different from the approach used in other studies, which used retrospective reporting based on hospital notes.

Derenne reported a P = 0.34 for the steroid course logistic regression analysis: "RR=0,80 {95%c.i. 0.23‐2.80, P=0.34}". The P value that we calculated, however, when using this RR with CIs, is 0.73, with the z‐value being 0.3450. We suggest that the z value and the P value might accidentally have been substituted in the publication.

The study reported a table of adverse events, which included the event “bronchitis”. We were uncertain as to what the term "bronchitis" meant in a trial on COPD, where COPD is commonly conceptualised as a chronic bronchitis. Both our expert and the paper's co‐author T. Similowski (Communication by email, 23/03/13) hypothesised that these were exacerbations, rather than pneumonias. As no information was provided in the paper on the definition of the term "bronchitis", we persisted with using the number of oral steroid courses as a more accurate reflection of exacerbations (this also being our protocol definition of exacerbation). As to our choice of steroid courses as opposed to antibiotic courses to represent exacerbations, the numbers were very similar and did not change the outcome.

Calverley 2010

The Calverley 2010 study was very well described. Funding and conflicts of interest were fully declared.

Regarding the inclusion criteria for participants, it is claimed that “GOLD” (Global Initiative for Obstructive Lung Disease) criteria were used. According to the description given in the paper, this is indeed the case, except for the small detail that postbronchodilator measurements, according to GOLD, have to be taken 10 to 15 minutes after administration of a short‐acting beta₂‐agonist (SABA) like salbutamol. The study used 30 minutes instead for the inclusion criterion. This is not expected to have influenced the actual result measurements, however, because for the study assessments, the study says, “Pulmonary function tests (FEV₁, FVC, …) were measured according to the American Thoracic Society/European Respiratory Society recommendation (Miller 2005)”. Calverley does not specify whether a SABA or a LABA was used as the bronchodilator for all of the postbronchodilator lung function tests, but if investigators adhered to the ATS/ERS guidelines, they would have performed the study assessments within 10 to 15 minutes of using a SABA, or within 30 minutes of using a LABA (Miller 2005, page 327).

For lung function measurements, Calverley repeatedly reports all predose, 3 hours postdose and peak measurements. Expert opinion was that the predose measurement was the most important. This is the “trough” measurement, which shows how well the treatment drug is working in the long term. Indeed, Calverley uses predose measurements in defining the primary aim of the study (under the heading "Sample size").

The other measurement of interest, but to a lesser degree, was the 3 hours postdose result. Expert opinion was that this would be a time frame chosen according to the pharmacodynamics of the treatment drugs to show maximal short‐term response.

Expert opinion was to reject the third category, peak measurement, as a measure open to bias.

Indeed Calverley confirmed this, saying, “I think there was some concern among the sponsors that the pre‐dose may not be the peak effect hence the other 2 secondary outcomes. ... it has been done in other studies so I did not mind collecting data for comparability assessments” (Personal communication by email, 27/2/13).

As this is the only study in the review so far that reported predose, 3 hours postdose and peak measurements, we included in the review only the most important measurement: the predose measurement. Neither Derenne 1995 nor Weir 1999 specifies to this extent which measurements were used for lung function in their studies, but predose measurements were likely used.

Please note that the terms "predose" and "postdose" describe the timing of lung function measurements in reference to administration of the trial drug on that day, not in reference to whether the measurements were pre‐bronchodilator or postbronchodilator. All lung function measurements in Calverley were postbronchodilator, as they were performed according to ATS/ERS guidelines (same above; Miller 2005), and Calverley confirmed by personal communication (email, 27/2/13) that postbronchodilator measurements were used.

Regarding adverse events (QTc interval evaluations, Holter monitoring, serum cortisol, plasma glucose, pneumonia), Calverley notes that their study alone was underpowered to exclude these rare events. A meta‐analysis such as this could clarify this part of the research question; however, except for pneumonia, only the Calverley study in this review reports on these outcomes.

The pneumonia statistic (which was noticeably higher for BDP/FF than for FF) was not highlighted in the paper, probably because Calverley, as stated above, said that the study was underpowered for these rare adverse events. However, it is of note that pneumonia is a very important outcome in COPD treatment studies, and there was no discussion on whether the difference between BDP/FF and FF was significant. Instead, the rates were only referred to in the discussion as “similar to that reported in placebo‐controlled trials using budesonide, where no pneumonia signals of concern have been observed over 1 year treatment (Sin 2009)”, with the actual numbers reported only in the accompanying online suppository of extra information. A further explanation for this lack of emphasis is that the data are described as "pneumonia as reported by patients".

As mentioned in Calverley 2010's own discussion, a low rate of exacerbations was noted overall compared with previous studies. Calverley 2010 cited two possible reasons for this: The closer follow‐up provided by physicians could have pre‐empted exacerbations, especially in East European countries, or selection bias could have led to inclusion of more stable participants because of the requirement for 3 months (2 months before inclusion and 4 weeks during the run‐in period) exacerbation‐free. This latter reason is cited by Wedzicha (FORWARD) 2013 as one of the reasons why they carried out their study.

A statistically significant increased rate ratio was noted for the mean rate of exacerbations leading to hospitalisation. This result may have reflected a type I error (a false‐positive effect). In this case, the study authors controlled for the variable 'country‐specific differences in hospitalisation procedures' by accounting for only length of actual hospital treatment for the exacerbations, not total duration of stay. The results of this post hoc analysis show no statistically significant differences (P = 0.607). Arguments for this result reflecting a type I error include the following.

• The third arm of the study, which also contained an ICS (budesonide/formoterol, i.e. BUD/FF), had a rate of hospitalised exacerbations (7) similar to that of the formoterol group (8), not similar to that of the beclometasone/formoterol group (13), as would be expected;

• The numbers of hospitalised exacerbations are low in all three arms of the study, leading to chance variation;

• The doses of ICS between the BDP/FF and BUD/FF arms should be roughly equivalent, as demonstrated in a previous trial that provided half the dose of each (Papi 2007);

• If BDP/FF and BUD/FF doses were not equivalent, the effect would be expected to be seen in the opposite direction, as the more potent ICS (extra‐fine particles in the BDP/FF pMDI inhaler vs the BUD/FF DPI inhaler) usually decreases, not increases, the incidence of exacerbations (Yang 2012); and

• For the other exacerbation‐related outcome measures ("patients with at least one exacerbation leading to hospitalisation"; "number of patients with at least one (non‐hospitalised) exacerbation"; "mean rate of (non‐hospitalised) exacerbations"), no statistically significant differences were reported.

Whether BDP/FF increases the risk of severe exacerbations compared with FF only is therefore debatable. For the sake of transparency and in the interest of reducing the risk of post hoc analysis bias, however, we disregarded the post hoc analysis.

The outcome self‐reported days without bronchodilator was assessed to be low in GRADE quality. This is because of the wide confidence intervals, the fact that self‐reported days is not the best way of assessing this outcome and because self‐reporting is open to introducing bias.

Potential biases in the review process

To minimise the impact of publication bias and to maximise the reliability of our review, we maximised the effort to obtain grey literature. We contacted authors of abstract‐only publications through any means possible to obtain the unpublished full text and were successful in most cases, including the ultimately included Derenne 1995 study. However, we still await the promised further details of the Weir 1999 analysis and the promised Vengerov 1998 full text.

Extra to the minimum requirements of analysing the Cochrane Airways Group Specialised Register search results, we searched conference proceeding databases and trial registers, obtained licensing information and contacted manufacturers.

As the only BDP versus placebo studies we found were an unpublished study (Derenne 1995) and a study published only with great difficulty as an extended conference proceeding (Weir 1999; revealed on communication with author P.S. Burge by email, 20/12/12; see Other potential sources of bias), we strongly suspected publication bias for this arm of our review.

We therefore even went beyond Cochrane methods in trying to determine the existence of unpublished trials by contacting ethics committees and licensing bodies to ask for clinical trial applications related to beclometasone in COPD. This was of particular importance for any potential studies (such as Derenne 1995) that went unpublished before the advent of trial registers after the turn of the century. This proved a difficult search query for most committees and organisations, who were not able to search very far back into the predigital era. As most of the medications used in medical practice today were licensed before the last decade, we suggest this is a problem for the reliability and transparency of the evidence base for many medicines currently in widespread use, such as beclometasone inhalers.

Both data extraction and the risk of bias assessment process were made more objective and accurate by having two people perform them (Higgins 2011). Bias assessment involves judgement calls and therefore introduces a layer of subjectivity. This is best reduced by having an additional person assess the paper. Data extraction, then, is prone to error if performed by one person only (Buscemi 2006).

No limitations were imposed on language. Therefore, a special effort was made with a Spanish record (Izquierdo 2003), which had to be obtained from the author, translated using Google Translate and screened for relevant articles. This led to the identification of the article Weir 1993, which was included in the independent assessment phase. Another example is a Chinese paper (Ouyang 1998), which had to be translated using Google Translate and with the help of an East Asian acquaintance. It was also excluded only at the assessment stage. Thus we tried to reduce any Anglosphere publication bias.

Google Translate is free and immediate and shows alternative translations for each sentence. It was very accurate and adept in construing faithful English sentences.

As well as being comprehensive, the search was systematic; each step was fully documented.

As a medical student, the primary review author DADC had no conflict of interest in presenting data to achieve significant findings but was concerned only with producing a project that met the highest feasible academic standards, independent of the results.

The selection criteria set in the protocol had some limitations. The required minimum number of people or a requirement for acceptable power was not prespecified. Neither did we include any detail regarding run‐in periods or medication or regarding co‐therapy with drugs other than ICS. For instance, in Thompson 1992, several participants were permitted to continue taking theophylline and beta₂‐agonists during the trial. The only mention of co‐therapy in the protocol involves a subanalysis of whether theophylline was used. This has now been clarified in Types of interventions.

The search strings improved with time, and therefore the searches lack consistency on two points: becodis* (intended to identify the now discontinued brand name Becodisk, Becodisks or the misspelling Becodisc) was added to all searches after 18/03/12, including the search of guideline.gov and OpenGrey.eu, but not CDSR, TRIP, CAGR, … Second, Fostair, a brand name for BDP/FF, is sometimes spelt as Foster, which came to the review authors’ attention only in May 2012. This alternative spelling should therefore have been included in all the searches.

It was not feasible with our resources to do a systematic review based on individual participant data. Hence we have used summary data, but we will reconsider when the Wedzicha (FORWARD) 2013 study is to be included. Combining this data with data from the Calverley 2010 study would be useful in evaluating our BDP/LABA versus LABA comparison. For BDP versus placebo, however, the Derenne 1995 data have been lost, and for Weir 1999, we still await the promised new summary data from the author.

Agreements and disagreements with other studies or reviews

No other systematic reviews are looking specifically at BDP among all ICS in COPD. We therefore compare against existing Cochrane reviews of all inhaled corticosteroids.

BDP versus placebo

In a Cochrane review comparing all ICS with placebo, Yang 2012 concludes that "clinicians should balance the potential benefits of inhaled steroids in COPD (reduced rate of exacerbations, reduced rate of decline in quality of life and possibly reduced rate of decline in FEV₁) against the potential side effects (oropharyngeal candidiasis and hoarseness, and risk of pneumonia)".

Similarly, the directions of the changes observed in this review for BDP versus placebo were seen as statistically non‐significant improvements in lung function and rate of exacerbations with statistically non‐significant higher occurrences of adverse events. We encountered a lack of data on pneumonia.

These similarities must naturally be interpreted with extreme caution, as our findings were not all statistically significant. However, it is possible that with additional study data (such as the Weir 1999 data), our confidence in the effect could increase to statistical significance.

The Yang 2012 review includes only the Derenne 1995 study as part of the aforementioned meta‐analysis (van Grunsven 1999). It includes the summary data of van Grunsven 1999 meta‐analytically whenever possible. It also fully includes the Weir 1999 study data, and the review authors reached conclusions in their risk of bias assessment that were different from ours.

BDP/LABA versus LABA

In comparison with the Cochrane review on the ICS/LABA combination versus LABA, Nannini 2012 concludes, "Concerns over the analysis and availability of data from the studies bring into question the superiority of ICS/LABA over LABA alone in preventing exacerbations. The effects on hospitalisations were inconsistent and require further exploration. There was moderate quality evidence of an increased risk of pneumonia with ICS/LABA. There was moderate quality evidence that treatments had similar effects on mortality. Quality of life, symptoms score, rescue medication use and FEV₁ improved more on ICS/LABA than on LABA, but the average differences were probably not clinically significant for these outcomes. To an individual patient the increased risk of pneumonia needs to be balanced against the possible reduction in exacerbations".

This review similarly concludes that statistically significant changes were found in lung function measurements and (self‐reported) days without rescue bronchodilators, which are unlikely to be clinically significant. We did find a statistically and clinically significant increased rate ratio of exacerbations leading to hospitalisation. We did not report statistically significant differences in our other outcomes, as were reported by the Nannini 2007 review, but it is suggested that the direction of the changes is similar. Additional study data, such as data derived from the Wedzicha (FORWARD) 2013 study, may improve our confidence in answering this question.

The Nannini 2012 review does not include our only included study in this arm (Calverley 2010).

Authors' conclusions

Implications for practice.

As current practice is to use BDP/LABA for stage 3 COPD, we will focus on this arm of the study to draw conclusions.

Upon balancing the benefits and harms, no clear evidence was found to support the benefit of using BDP/LABA inhalers over LABA alone. Three outcomes reached 95% statistical significance (lung function, mean rate of exacerbations leading to hospitalisation and rescue bronchodilator frequency). This increased rate of severe exacerbations is open to interpretation, whereas lung function and rescue inhaler usage effect sizes are small and are unlikely to be clinically significant.

The quality of evidence of our primary outcomes ranged from high (lung function) to low and very low (pneumonia and mortality, respectively), but the other outcomes (including exacerbations) were mainly of moderate quality.

Although most patients will not experience any benefit of taking BDP/LABA compared with LABA, any given individual may do. The mean effect is the average of an unknown distribution and does not rule out the possibility of some individuals obtaining clinically important benefits.

The values and preferences of the patient should be taken into account when decision is made whether to prescribe these inhalers. It is worth reminding that BDP and BDP/LABA are currently unlicensed for use in COPD in many countries, so clinicians should exercise care in their use and should discuss this with their patients.

We did not conduct a cost‐effectiveness analysis, so we cannot comment on implications for resource allocations. However, although BDP is cheaper than other ICS drugs, clinicians should be mindful of the lack of effectiveness data on hospitalisation—the primary cost driver with this disease.

Implications for research.

We await the publication of another trial comparing BDP/LABA with LABA (Wedzicha (FORWARD) 2013), which is likely to be included. This may increase our confidence in some of the results.

The research included in this review was conducted in participants with stage 3 COPD. More research is needed to look at the effectiveness of BDP/LABA in different stages of COPD.

An adequately powered head‐to‐head study of BDP versus the more potent ICS in combination with LABAs using important outcomes for participants such as hospitalisation might identify substantial cost savings for health services.

To address the long‐term benefits and harms of BDP/LABA (mortality, adverse events), research with higher power and with a longer follow‐up period is needed. This may be more feasible with the use of observational cohort studies.

Last, we hope this review will stimulate future reviews that will look separately at the other ICS in COPD, so that these can be compared in an overview.

Appendices

Appendix 1. Sources and search methods for the Cochrane Airways Group Specialised Register (CAGR)

Electronic searches: core databases

Database	Frequency of search
MEDLINE (Ovid)	Weekly
EMBASE (Ovid)	Weekly
CENTRAL (The Cochrane Library)	Quarterly
PsychINFO (Ovid)	Monthly
CINAHL (EBSCO)	Monthly
AMED (EBSCO)	Monthly

 

Handsearches: core respiratory conference abstracts

Conference	Years searched
American Academy of Allergy, Asthma and Immunology (AAAAI)	2001 onwards
American Thoracic Society (ATS)	2001 onwards
Asia Pacific Society of Respirology (APSR)	2004 onwards
British Thoracic Society Winter Meeting (BTS)	2000 onwards
Chest Meeting	2003 onwards
European Respiratory Society (ERS)	1992, 1994, 2000 onwards
International Primary Care Respiratory Group Congress (IPCRG)	2002 onwards
Thoracic Society of Australia and New Zealand (TSANZ)	1999 onwards

 

COPD search

1. Lung Diseases, Obstructive/

2. exp Pulmonary Disease, Chronic Obstructive/

3. emphysema$.mp.

4. (chronic$ adj3 bronchiti$).mp.

5. (obstruct$ adj3 (pulmonary or lung$ or airway$ or airflow$ or bronch$ or respirat$)).mp.

6. COPD.mp.

7. COAD.mp.

8. COBD.mp.

9. AECB.mp.

10. or/1‐9

Filter to identify RCTs

1. exp "clinical trial [publication type]"/

2. (randomised or randomised).ab,ti.

3. placebo.ab,ti.

4. dt.fs.

5. randomly.ab,ti.

6. trial.ab,ti.

7. groups.ab,ti.

8. or/1‐7

9. Animals/

10. Humans/

11. 9 not (9 and 10)

12. 8 not 11

The MEDLINE strategy and the RCT filter are adapted to identify trials in other electronic databases.

Appendix 2. Checklist of items to consider in data collection or data extraction

Source Study ID (created by review author) Report ID (created by review author) Review author ID (created by review author) Citation and contact details Eligibility Confirmed eligibility for review Reason for exclusion Methods Study design Total study duration Length of follow‐up Cochrane bias tool Participants Total number Setting Diagnostic criteria (according to GOLD or other) Age Country Comorbidity (respiratory diseases and conditions likely to cause death within 3 years) Date of study Interventions Total number of intervention groups BDP by MDI, DPI or spacer? For each intervention and comparison group of interest Specific intervention  Intervention details (sufficient for replication, if feasible)

Outcomes Outcomes and time points (i) collected; (ii) reported For each outcome of interest Outcome definition (with diagnostic criteria if relevant) Unit of measurement (if relevant) For scales: upper and lower limits, and whether high score is good Results Number of participants allocated to each intervention group For each outcome of interest Sample size Missing participants Summary data for each intervention group (e.g. 2 × 2 table for dichotomous data; means and SDs for continuous data) Estimate of effect with confidence interval; P value Subgroup analyses Miscellaneous Funding source Key conclusions of the study authors Miscellaneous comments from the study authors References to other relevant studies Correspondence required Miscellaneous comments by the review authors

Appendix 3. The Cochrane Collaboration’s tool for assessing risk of bias

Domain	Support for judgement	Review authors’ judgement
Random sequence generation (selection bias)	Describe in sufficient detail the method used to generate the allocation sequence to allow an assessment of whether it should produce comparable groups	Selection bias (biased allocation to interventions) due to inadequate generation of a randomised sequence
Allocation concealment (selection bias)	Describe in sufficient detail the method used to conceal the allocation sequence to determine whether intervention allocations could have been foreseen in advance of, or during, enrolment	Selection bias (biased allocation to interventions) due to inadequate concealment of allocations before assignment
Blinding of participants and personnel (performance bias) Assessments should be made for each main outcome (or class of outcomes)	Describe all measures used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. Provide any information related to whether the intended blinding was effective	Performance bias due to knowledge of the allocated interventions by participants and personnel during the study
Blinding of outcome assessment (detection bias)Assessments should be made for each main outcome (or class of outcomes)	Describe all measures used, if any, to blind outcome assessors from knowledge of which intervention a participant received. Provide any information related to whether the intended blinding was effective	Detection bias due to knowledge of the allocated interventions by outcome assessors
Incomplete outcome data (attrition bias)Assessments should be made for each main outcome (or class of outcomes)	Describe the completeness of outcome data for each main outcome, including attrition and exclusions from the analysis. State whether attrition and exclusions were reported, the numbers in each intervention group (compared with total randomly assigned participants), reasons for attrition/exclusions when reported and any re‐inclusions in analyses performed by the review authors	Attrition bias due to amount, nature or handling of incomplete outcome data
Selective reporting (reporting bias)	State how the possibility of selective outcome reporting was examined by the review authors, and describe what was found	Reporting bias due to selective outcome reporting
Other sources of bias	State any important concerns about bias not addressed in the other domains in the tool If particular questions/entries were prespecified in the review’s protocol, responses should be provided for each question/entry	Bias due to problems not covered elsewhere in the table

Data and analyses

Comparison 1. Beclometasone versus placebo.

Outcome or subgroup title	No. of studies	No. of participants	Statistical method	Effect size
1 Change in FEV1	1		Mean Difference (IV, Fixed, 95% CI)	Totals not selected
1.1 At 1 year	1		Mean Difference (IV, Fixed, 95% CI)	0.0 [0.0, 0.0]
1.2 At 2 years	1		Mean Difference (IV, Fixed, 95% CI)	0.0 [0.0, 0.0]
2 Mortality (dichotomous Peto method)	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	Totals not selected
2.1 All‐cause	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]
2.2 Respiratory	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]
3 Exacerbations: mean rate (rate ratio)	1		Rate Ratio (Fixed, 95% CI)	Totals not selected
4 Symptoms: change in dyspnoea scale (Fletcher Scale)	1		Mean Difference (IV, Random, 95% CI)	Totals not selected
5 Adverse events	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	Totals not selected
5.1 Candidiasis	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]
5.2 Dysphonia	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]
5.3 Bone fractures	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]
6 Withdrawal	2		Peto Odds Ratio (Peto, Fixed, 95% CI)	Subtotals only
6.1 All‐cause	2	292	Peto Odds Ratio (Peto, Fixed, 95% CI)	1.33 [0.83, 2.14]
6.2 Due to adverse events	1	194	Peto Odds Ratio (Peto, Fixed, 95% CI)	1.06 [0.52, 2.19]
6.3 Due to ineffectiveness of treatment	2	292	Peto Odds Ratio (Peto, Fixed, 95% CI)	1.55 [0.60, 4.04]

1.2. Analysis.

Comparison 1 Beclometasone versus placebo, Outcome 2 Mortality (dichotomous Peto method).

1.4. Analysis.

Comparison 1 Beclometasone versus placebo, Outcome 4 Symptoms: change in dyspnoea scale (Fletcher Scale).

1.5. Analysis.

Comparison 1 Beclometasone versus placebo, Outcome 5 Adverse events.

Comparison 2. Beclometasone/formoterol versus formoterol.

Outcome or subgroup title	No. of studies	No. of participants	Statistical method	Effect size
1 Change in FEV1	1		Mean Difference (IV, Fixed, 95% CI)	Totals not selected
2 Mortality (all‐cause) (dichotomous Peto method)	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	Totals not selected
2.1 All‐cause	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]
2.2 Respiratory	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]
3 Pneumonia: participants with at least one (dichotomous Peto odds ratios)	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	Totals not selected
4 Change in exercise capacity: 6MWT	1		Mean Difference (IV, Fixed, 95% CI)	Totals not selected
5 Exacerbations: participants with at least one (dichotomous)	1		Odds Ratio (M‐H, Fixed, 95% CI)	Totals not selected
6 Exacerbations (hospitalisations): participants with at least one (dichotomous)	1		Odds Ratio (M‐H, Fixed, 95% CI)	Totals not selected
7 Exacerbations (hospitalisations): mean rate (rate ratio)	1		Rate Ratio (Fixed, 95% CI)	Totals not selected
8 Number of hospitalisations (rate ratio)	1		Rate Ratio (Fixed, 95% CI)	Totals not selected
9 Change in Quality of Life: SGRQ	1		Mean Difference (IV, Fixed, 95% CI)	Totals not selected
10 Symptoms: change in dyspnoea scale (modified Medical Research Council questionnaire)	1		Mean Difference (IV, Random, 95% CI)	Totals not selected
11 Symptoms: change in BODE index	1		Mean Difference (IV, Random, 95% CI)	Totals not selected
12 Use of rescue bronchodilators: self‐reported days without	1		Mean Difference (IV, Random, 95% CI)	Totals not selected
13 Adverse events	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	Totals not selected
13.1 Candidiasis	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]
13.2 Dysphonia	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]
13.3 Bone fractures	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]
14 Withdrawal	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	Totals not selected
14.1 All‐cause	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]
14.2 Due to adverse events	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	0.0 [0.0, 0.0]

2.1. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 1 Change in FEV₁.

2.2. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 2 Mortality (all‐cause) (dichotomous Peto method).

2.3. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 3 Pneumonia: participants with at least one (dichotomous Peto odds ratios).

2.4. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 4 Change in exercise capacity: 6MWT.

2.5. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 5 Exacerbations: participants with at least one (dichotomous).

2.6. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 6 Exacerbations (hospitalisations): participants with at least one (dichotomous).

2.7. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 7 Exacerbations (hospitalisations): mean rate (rate ratio).

2.8. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 8 Number of hospitalisations (rate ratio).

2.9. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 9 Change in Quality of Life: SGRQ.

2.10. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 10 Symptoms: change in dyspnoea scale (modified Medical Research Council questionnaire).

2.11. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 11 Symptoms: change in BODE index.

2.12. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 12 Use of rescue bronchodilators: self‐reported days without.

2.13. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 13 Adverse events.

2.14. Analysis.

Comparison 2 Beclometasone/formoterol versus formoterol, Outcome 14 Withdrawal.

Characteristics of studies

Characteristics of included studies [ordered by study ID]

Calverley 2010.

Methods	Parallel, double‐blind, randomised trial. Duration: 48 weeks and 4 weeks of run‐in (52 weeks in total)
Participants	1. Total number randomly assigned 476 (BDP/FF 237, FF 239). Additional treatment groups not covered in this review: BUD/FF 242 2. Setting: 76 centres in 8 European countries (Bulgaria, France, Italy, Poland, Russia, Spain, Ukraine, United Kingdom) 3. Diagnostic criteria (according to GOLD or other): claims “GOLD” criteria and this is accurate save for a small detail: The study required a 30‐minute postbronchodilator (post‐BD) change in FEV1 of < 12% (although GOLD guidelines specify 10 to 15 minutes post‐BD). Other inclusion criteria: age ≥ 40; > 2 years diagnosis of symptomatic COPD; post‐BD 30% < FEV1 < 50% of the predicted normal; ≥ 0.7 L FEV1; ≥ 1 exacerbation (with oral CS and/or antibiotics and/or visit to emergency department and/or hospitalisation) within 2 to 12 months before screening; clinically stable for 2 months before study Baseline characteristics of postbronchodilator FEV1 were: BDP/FF 41.9 ± 5.6 % and LABA 42.5 ± 5.9%. 4. Age 63.0 ± 9.0 and 63.7 ± 8.8 5. Comorbidity: no asthma, allergic rhinitis or atopic disease, diurnal symptoms suggesting asthma 6. Smoking status: ≥ 20 pack‐years smoking history; smokers and ex‐smokers (baseline characteristics: smokers/ex‐smokers: BDP/FF 90/142, FF 87/146; number of packs per year (SDs): BDP/FF 37.3 (14.1), FF 39.7 (19.1))
Interventions	Run‐in: ipratropium/salbutamol (20/100 µg, 2 puffs TDS) Total number of intervention groups: 3 (2 relevant) MDI, DPI or spacer? pMDI for BDP/FF, DPI for FF Co‐pharmacy? All COPD treatments were discontinued after the run‐in, except for rescue inhaler (salbutamol PRN)   1. Beclometasone/formoterol pMDI 100/6 µg, 2 puffs BD (so daily dose 400/24) (Foster, Chiesi) 2. Formoterol DPI 12 µg, 1 puff BD (so daily dose 24) (Oxis, AstraZeneca)
Outcomes	1. Pulmonary function tests (FEV1 of interest), according to ATS/ERS 2. COPD exacerbations (defined as need for treatment with oral corticosteroids and/or antibiotics and/or the need to visit or be admitted to a hospital) Number of participants with at least one exacerbation Mean rate of exacerbations 3. Dyspnoea scores (Modified Medical Research Council questionnaire) (Mahler 1988) High score is bad 4. Quality of life (SGRQ) High score is bad 5. Exercise capacity (6MWT) High score is good (longer distance) 6. Body Mass Index, airflow Obstruction, Dyspnoea and Exercise capacity (BODE) Index. (Celli 2004) High score is bad 7. Use of rescue bronchodilator Unit: inhalations/d 8. Adverse events: I. QTc interval evaluations, ii. Holter monitoring, iii. Serum cortisol, iv. Plasma glucose, v. Pneumonia, vi. Adverse event (AE) statistics 9. Withdrawal (reviewer’s outcome): I. all cause, ii. due to AEs 10. Outcome definition: mortality I) all cause, ii) respiratory
Notes	Date of study: December 2006 to August 2008 Funding: Chiesi
Risk of bias
Bias	Authors' judgement	Support for judgement
Random sequence generation (selection bias)	Low risk	Quote: "The IXRS assigned the patient to a certain treatment group using a list‐based randomisation algorithm" Comment: IXRS is a computer‐based system (see below)
Allocation concealment (selection bias)	Low risk	Quote: "Patients were centrally assigned, in each centre, to one of the three treatment arms at the end of the run‐in period through an Interactive Voice/Web Response System (IXRS)"
Blinding of participants and personnel (performance bias) All outcomes	Low risk	Quote: "Almac Clinical Technologies (UK) was in charge of the IXRS study drug management. The investigators at the sites called the IXRS to screen and randomise patients"
Blinding of outcome assessment (detection bias) All outcomes	Low risk	Quote: "Study drug was kitted and uniquely numbered and the IXRS was used to assign both initial and subsequent kits in order to have an inventory control and patient dose tracking. The IXRS also maintained quantities, kit numbers, drug types, batch/code numbers, expiration dates and did not dispense after these dates. On each study day, patients took both active medications and matched placebo twice daily, in order to maintain blinding"
Incomplete outcome data (attrition bias) All outcomes	Low risk	Quote: "Missing values were accounted for using the last observation carried forward (LOCF) approach" Comment: The LOCF was deemed by us as an acceptable manner of imputing data in the difficult area of imputing data in ITT analyses Withdrawal reasons were extensively reported. Two participants seemed missing from randomisation when the Consort Flow Diagram was scrutinised (Both the total N of BDP/FF and the total N of FF are different from the breakdown into N withdrawn and N completed) Calverley PM responded to this query by saying that this was due to the strict reporting rules—Calverley P thinks these were two participants who were randomly assigned but never received study medication. Furthermore, we deemed that two participants missing out of 476 (237 ± 239) is unlikely to affect outcomes
Selective reporting (reporting bias)	Low risk	Although no full protocol was available, a national trial registry entry appeared on clinicaltrials.gov. Review of this entry revealed the following: All protocol outcomes were included. One country (Germany) was not mentioned in the final paper. When the authors Professors Peter M Calverley and Stefano Petruzzelli, Chief Medical Officers of Chiesi, were emailed, they clarified that German centres did not recruit participants, as although the German Regulatory Authority approved the study, some questions related to the comparator arm (formoterol alone) were raised by ethics committees
Other bias	Low risk	Possible conflict of interest: funding provided by Chiesi. Two of the authors are employed by Chiesi However, these conflicts of interest were declared. The main author is an expert in the field and has conducted trials for several competing manufacturers

Derenne 1995.

Methods	Randomised placebo‐controlled multicentre trial. Duration: 2 years
Participants	1. Total number: 194 (100 BDP, 94 PL) 2. Setting: 28 outpatient lung clinics in France 3. Diagnostic criteria: ATS 1987 (chronic bronchitis: cough + sputum most days for minimum of 3 consecutive months in 2 consecutive years) Prebronchodilator FEV1 30% to 60% of predicted (Quanjer 1983) 10 minutes postbronchodilator FEV1 increase < 15% predicted (FEV1) Further assessment at end of run‐in: pre‐BD FEV1 not different by > 10% from pretrial FEV1 +  IgE < 200 IU and/or blood eosinophils < 500/mm3 + PaO2 ≥ 55 mm Hg. Baseline characteristics of postbronchodilator FEV1 were: BDP 51 ± 12% and PL 48 ± 11%. 4. Age: < 75 years 5. Comorbidity: exclusion: history of severe exacerbations of COPD past 3 months; lung cancer/bullous emphysema/asthma or history suggestive of asthma in past 10 years; long‐term use of ICS; oral corticosteroids in past 15 days; inability to follow protocol, participation in other trial; pregnant/lactating; stomach ulcer without treatment; pulmonary TB; unable to use inhaler 6. Smoking status: both smokers and non‐smokers (baseline characteristics: current/former/non‐smoker: BDP 27/62/11; PL 28/56/10. Pack‐years (SDs): BDP 37 (27); PL 41 (28))
Interventions	Run‐in: 2‐week period maintaining participants' usual treatments (anticholinergics, beta2‐agonists, theophylline, mucolytics, almitrine) Total number of intervention groups: 1 MDI, DPI or spacer? MDI Co‐pharmacy: 1. Antibiotics (max 15 days): in case of exacerbation 2. Prednisone orally: on investigator’s judgement (e.g. in case of increased dyspnoea) 3. No complete certainty from article or correspondence that participants' usual regimens (anticholinergics, beta2‐agonists, theophylline, mucolytics, almitrine) were discontinued after run‐in period (baseline characteristics (% of subjects): anticholinergics BDP 19%, PL 22%; beta2‐agonists BDP 59%, PL 61%; theophylline BDP 58%, PL 61%; mucolytics BDP 40%, PL 48%; almitrine BDP 10%, PL 17%) Interventions: 1. Beclometasone dipropionate (Becotide) 1500 μg (3 puffs of 250 μg BD) 2. Placebo
Outcomes	Outcomes and time points: I. collected, ii. reported 1. “Reversibility” of lung function tests: post‐BD FEV1 I. Every half year, stated elsewhere as “assessed annually” Outcome definition: FEV1 (as % of FEV1 predicted) 10 minutes after 4 puffs 100 μg salbutamol Unit of measurement: % of FEV1 predicted Limits: 0‐100%. High score is good 2. Number of exacerbations I. Every three months (each follow‐up visit) Outcome definition: prescribed courses of antibiotics or oral corticosteroids NB: Patients were told to come to the clinic to have exacerbation diagnosed if they noticed increased mucopurulent sputum and fever 3. Symptom: dyspnoea I. At baseline, 3, 6, 12, 18 and 24 months Outcome definition: 1 = no dyspnoea, 2 = no dyspnoea when walking on flat ground, 3 = no dyspnoea when walking slowly, 4 = dyspnoea even when walking slowly, 5 = dyspnoea while undressing Unit of measurement: Fletcher Scale (Fletcher 1964) Limits of scale: 1 to 5. High score is bad 4. Hospitalisation and duration I. Every three months (each follow‐up visit) Outcome definition: n/a 5. Adverse events I. At every visit (three months or in between) Outcome definition: “... at each visit, the subjects were asked if the drug of treatment was well tolerated and if not, the investigator had to fill in a standard (serious) adverse event form” 6. Withdrawal (reviewer’s own outcome) ii. At end of 24 months 7. Mortality (reviewer’s own outcome) (all‐cause and respiratory) ii. At 24 months
Notes	Date of study: 15 May 1989 to 9 February 1990 Funding: GlaxoWellcome Pharmaceutical
Risk of bias
Bias	Authors' judgement	Support for judgement
Random sequence generation (selection bias)	Unclear risk	Quote: "Block randomisation was performed". Comment: As Chapter 8.9.2.3 states (Higgins 2011), this inadequate level of reporting requires a judgement of "unclear risk"
Allocation concealment (selection bias)	High risk	Quote: "Each of the investigators was given a set of 8 sealed envelopes containing the assignment codes" Comment: Although they are described as "sealed" envelopes, no details on opacity or sequential numbering of the envelopes are provided
Blinding of participants and personnel (performance bias) All outcomes	Unclear risk	Quote: "At each visit, a box with 8 MDI's, sufficient for 3 months, was supplied" Comment: Other than this quote, no more description provided, leaving unanswered questions such as: Who provided the MDI? Was it an independent body? Who was in charge of labelling with the assignment codes?
Blinding of outcome assessment (detection bias) All outcomes	Unclear risk	Quote: "The code could be broken in the event of a serious adverse event" Comment: This implies that throughout the study, the assessors could find out who was actually being treated only if they had to go back to break the assignment code. Quote:"All measurements were taken with the same apparatus, and if possible, with the same technician and at the same time of day." Comment: Although this sentence is mainly intended to indicate how the risk of measurement error was reduced, it may also imply that the researchers reduced the risk of treating the placebo and treatment groups differently However, both these quotes lead to conclusions drawn by implication, as the subject of blinding is not addressed in the study. This would not matter for objective outcome measures (pulmonary function tests, blood gasses, dyspnoea, hospitalisations, consultations) but could have an impact on subjective measures (general well‐being [both physician and participant assessed], smoking behaviour, corticosteroid and antibiotic courses)
Incomplete outcome data (attrition bias) All outcomes	High risk	Quote: "...due to missing values in the multivariate model [of FEV1], which corrected for possible confounding variables, the number of measurements which were to be included was strongly reduced. The better result in terms of postbronchodilator FEV1 compared to pre‐bronchodilator FEV1 should therefore be considered with due caution" Comment: It is odd to see multivariate analysis in an RCT—presumably as the randomisation did not work too well (i.e.the groups were not the same at baseline)
Selective reporting (reporting bias)	Low risk	Comment: A protocol is not available, but another version of the abstract is available in the form of the conference abstract published as a supplement in the American Journal of Respiratory and Critical Care Medicine. Compared with the full text, FEV1 outcomes are reported separately as deviations from baseline in placebo and treatment groups, and the other outcome in the abstract is the peak expiratory flow, which is known to be not helpful in COPD. This abstract may have consisted of preliminary findings The full text, however, although it also concentrates on outcomes that are not of interest (e.g. pre‐bronchodilator FEV1 measures) does not seem to withhold outcomes of interest (e.g. postbronchodilator FEV1 in treatment group vs placebo group)
Other bias	Low risk	Quote: "This study was originally coordinated by one of the co‐authors (J.P. Derenne) in cooperation with GlaxoWellcome France. So far, its results have only been presented in abstract form and have not been published in full. The study was selected for a meta‐analysis of published and unpublished studies on the long‐term effects of inhaled corticosteroids in COPD. Here, we present the full analysis of the original raw data to avoid publication bias and the restrictions imposed by the meta‐analysis" Comment: funding declared. As this is an original document instead of a peer‐reviewed publication, risk of publication bias should be low

Weir 1999.

Methods	Randomised placebo‐controlled double‐blind parallel‐group trial Duration: 2 years
Participants	1. Total number: 98 participants randomly assigned, 78 completing at least 12 months of treatment, 59 completing the 2‐year study period 2. Setting: Quote: “The patients entered into the study reflect the majority of those presenting to an urban chest clinic with COPD, where the major pathology is smoking‐related” 3. Diagnostic criteria: clinical diagnosis of COPD, adult‐onset airflow obstruction with FEV1 < 70% predicted and FEV1/FVC < 65%. Excluded if clinically significant BD reversibility; history of acute attacks of breathlessness with recovery between attacks; significant improvement with steroid treatment in the past; if steroid treatment clinically indicated, any form of corticosteroid therapy prescribed for > 3 months in previous year; any steroids prescribed in 4‐week run‐in. Baseline characteristics of postbronchodilator FEV1 were reported in Litres as BDP 1.19 ± 0.07L and PL 1.26 ± 0.07. We estimated that this was equivalent to FEV1 42.7% predicted for BDP and 45% for PL. 4. Age: 67.6 (SEM 1.0) and 65.5 (SEM 1.0) years 5. Comorbidity: no clinical diagnosis of asthma 6. Smoking status: smokers and ex‐smokers (baseline characteristics: smokers/ex‐smokers: BDP 17/31, PL 21/28; number of packs per year (SEMs): BDP 54 (9), PL 56 (8))
Interventions	Run‐in: none Total number of intervention groups: 1 MDI, DPI or spacer: MDI with spacer Co‐pharmacy: rescue inhalers as required. Participants receiving theophylline continued (no change of dose during trial) Interventions: 750 μg BD of BDP if weight < 50 kg; 1000 μg BD if > 50 kg Placebo inhaler; an equivalent number of puffs, as determined by body weight
Outcomes	1. Change in post‐BD FEV1 2. Rate of exacerbations (exacerbation not defined) Unit: number/y 3. Change in BDI (Baseline Dyspnoea Index) (Mahler 1988) 4. Chronic Respiratory Disease Questionnaire (Guyatt 1987) (subgroup of participants) (data declared as not reported in this publication) 5. Withdrawal (reviewer’s own outcome)
Notes	No ITT analysis (Quote: “Only patients with data points for at least 12 months were included in the final analysis”) Funding: undeclared in the publication. "The study was unfunded, except that GlaxoWellcome provided the drugs and placebo and did the randomisation" (P.S. Burge, 20/12/12, communication by email) "...the analysis of the CRF/lung function" (CRF: Clinical Record Folder (the source data)) "was done by Dr RK Sharma International Clinical Research manager of Glaxo" (P.S. Burge, 26/2/13, communication by email) Correspondence required: number of participants for each arm used in the analysis (i.e. lasted > 12 mo). Details on random allocation. Details on methods for Cochrane bias tool. Details on matching. Original data if possible for an ITT analysis. Details on what constitutes an exacerbation. Details of conflicts of interest
Risk of bias
Bias	Authors' judgement	Support for judgement
Random sequence generation (selection bias)	Unclear risk	Quote: "The study was a randomised placebo‐controlled double‐blind parallel group comparison..." Comment: insufficient information on sequence generation. Furthermore, when the author P.S. Burge was emailed, he could not give further details on which method of random sequence generation was used
Allocation concealment (selection bias)	Low risk	Comment: no detail in the study. However, as emailed by author P.S. Burge, "I cannot find out how randomisation was done within blocks, this was done by GSK, we entered patients serially having already received the inhalers which all looked identical but were numbered, the study was double blind." So, evidence of central allocation and sequentially numbered drug inhalers of identical appearance
Blinding of participants and personnel (performance bias) All outcomes	Low risk	Quote: "The study was a randomised placebo‐controlled double‐blind parallel group comparison..." Quote: "...each patient having all measurements on the same machine throughout the study" Comment: Participants were treated in the same way. As above, as emailed by P.S. Burge, inhalers looked the same, received from a central body. So neither participant nor investigator could know which was which
Blinding of outcome assessment (detection bias) All outcomes	Low risk	Quote: "All lung function measurements were made on regularly calibrated dry bellows spirometers at the same time of the day, each patient having all measurements on the same machine throughout the study" Comment: As above quotes illustrate, measurement was the same for both groups
Incomplete outcome data (attrition bias) All outcomes	High risk	Quote: "Only patients with data points for at least 12 months were included in the final analysis" Comment: This is not an intention‐to‐treat analysis, and therefore it is at high risk of introducing bias Quote: "The 39 patients withdrawn from the study had significantly worse airflow obstruction than the 59 patients completing the study [mean (SEM) baseline FEV1 (litres): withdrawn group 0.93 (0.07), completers 1.21 (0.06), P < 0.01]. Only three patients in the active treatment group and six in the placebo were withdrawn because they experienced two exacerbations in a 3‐month period. There were no significant differences in total withdrawal rates for any reason between the two treatment groups" Comment: As is the problem with many COPD steroid studies, participants withdrew because of lack of effective treatment in both placebo and treatment groups. As withdrawn participants had significantly worse lung function, this could introduce risk of bias in the outcome measurements The last sentence was clarified with the authors to mean that no significance was found in the total withdrawal rates for any given reason, as well as no significant difference for all‐reason withdrawal. As withdrawal is balanced across both groups, risk of bias is minimised. Furthermore, six placebo participants—more than three beclometasone participants—would be likely to underestimate treatment effect of beclometasone, thereby decreasing the risk of bias
Selective reporting (reporting bias)	Unclear risk	Quote: "A subgroup of patients also answered the Chronic Respiratory Disease Questionnaire of Guyatt et al. [7], although these data are not reported here" Comment: P.S. Burge informed us (26/2/13) that "The reason that the Guyatt questionnaire was not used on all is due to lack of staff for a period, i.e. selection was by date of clinics rather than anything medical. (...) The Guyatt data was to be analysed by our clinical nurse specialist, Geraldine Bale. There are several published abstracts of this" Despite corresponding with Geraldine Bale (now Geraldine Burge), we were unable to identify any abstracts with numerical reporting of questionnaire results in the text Comment: No information was provided on how many participants were in each arm of the analysis, rendering data unusable for entry into a meta‐analysis
Other bias	High risk	No information declared on sponsorship, yet correspondence with P.S. Burge revealed involvement of GSK in the block randomisation process, provision of the study drugs and analysis, so GSK is likely funder No information on conflicts of interest. For these two reasons alone, this study has been deemed at high risk for "other bias" Quote: "Patients taking oral theophyllines maintained a constant dose throughout the study period" Comment: Co‐pharmacy was present in the study for recruited participants who were taking theophylline before the start of the trial. Theophylline is a recognised treatment in COPD (GOLD 2010) and has been shown to significantly improve FEV1 and FVC (Ram 2002). It was not specified for how many participants this was the case, nor how many were in each treatment arm, leading to an assessment of unclear risk of further performance bias

Characteristics of excluded studies [ordered by study ID]

Study	Reason for exclusion
Boothman‐Burrell 1997	Primary reason: inadequate inclusion criteria. Inclusion criterion of < 25% reversibility to bronchodilator too broad to exclude asthmatic patients. Secondary reasons: 1 month washout period too short to use the first treatment period as a parallel study, further made impossible by the ten days of prednisone administered after the first treatment period
Dinc 2001	Not a randomised trial. Observational study
John 2005	No data available beyond the published data. Because our expert opinion was that the washout period of 4 weeks was to short (i.e. < 6 weeks), this cross‐over study was to be treated as a parallel study. However, the authors communicated with us that data for the first treatment period only could not be supplied
Miravitlles 2002	Not a randomised trial. Observational study
Ouyang 1998	Not double‐blinded. Single‐blind
Shmelev 2006	Not double‐blinded. No blinding at all
Struijs 1997	Not a randomised trial. No randomisation into placebo
Thompson 1992	Treatment less than 12 weeks. 6 weeks only
Tzani 2011	Not correct research question. Comparison of beclometasone with fluticasone, not with placebo
van Schayck 1995	Not a randomised controlled trial
Weir 1990	Treatment less than 12 weeks. 2 weeks only
Weir 1993	Treatment less than 12 weeks. 3 weeks only

Characteristics of studies awaiting assessment [ordered by study ID]

Vengerov 1998.

Methods	Randomised prospective trial. Duration: 5 years (blinding not stated in abstract)
Participants	1. Total number: 89 men (45 BDP, 44 control) 2. Setting: metal workers in Ukraine (industrial pollutants with extremely irritating activity) 3. Diagnostic criteria: COPD, males, non‐smokers, initial FEV1 46% to 70% predicted 4. Age: mean age 43.6 years 5. Comorbidity: not stated in abstract
Interventions	1. 750 to 1250 μg beclometasone dipropionate (Becotide/Becloforte) daily 2. Observation as control group
Outcomes	1. Change in FEV1 2. Number of exacerbations ("relapses") and length of stay in hospital 3. Symptom score 4. Bronchofibroscopic degree of inflammation
Notes	Abstract only. Awaiting full text

Characteristics of ongoing studies [ordered by study ID]

Wedzicha (FORWARD) 2013.

Trial name or title	48‐Week, Double Blind, Randomized, Multinational, Multicentre, "Fixed Combination" Beclomethasone Dipropionate Plus Formoterol Fumarate Versus Formoterol in Patients With Severe Chronic Obstructive Pulmonary Disease
Methods	Randomised, double‐blind, parallel‐group trial Duration: 48 weeks
Participants	1. Total number: 1119 participants enrolled 2. Setting: multinational, multicentre (Germany, Austria, Ireland, UK, Czech Republic) 3. Inclusion criteria: Severe COPD At least one COPD exacerbation in previous year Exclusion criteria: Asthma, allergic rhinitis or other atopic disease Unstable concurrent disease Evidence of heart failure 4. Age. > 40 years
Interventions	Run‐in. Information not available (N/A) Total number of intervention groups: 2 MDI, DPI or spacer? MDI Co‐pharmacy? N/A Interventions: Beclometasone dipropionate 100 µg plus formoterol fumarate 6 µg per metered dose combination inhaler (Foster, Fostair) Formoterol fumarate 12 µg per metered dose (Atimos)
Outcomes	Primary Exacerbation rate Change in predose FEV1 Secondary Pulmonary function parameters (FEV1/FVC) Saint George’s Respiratory Questionnaire Use of rescue medication
Starting date	October 2009
Contact information	Jadwiga A Wedzicha, MD, Prof, UCL Medical School
Notes	Funded by Chiesi Estimated study publishing date: August 2013

Differences between protocol and review

We clarified that we would consider studies with concomitant therapy in Types of interventions, which was only implied previously by the provision of a subgroup analysis.

We updated the Search methods for identification of studies to reflect the much wider search that we performed than was planned per protocol.

Under Searching other resources, we deleted "We will contact ... experts in the field", as we asked that the final review be reviewed by our own expert in the field.

Contributions of authors

DADC drafted the protocol with input from MJ and our expert. DADC and NT screened the search results based on title and/or abstract. DADC and MJ screened full texts for inclusion and extracted data. DADC and NT performed bias assessments of included studies. When any difference arose between DADC and NT, MJ was consulted, and further expert opinion was obtained. DADC performed the analysis with input from the Cochrane Airways Group when uncertainties arose.

Sources of support

Internal sources

• New source of support, Not specified.

External sources

• No sources of support supplied

Declarations of interest

The authors DADC, MJ and NT have no connections with any organisation that might have a conflict of interest; they are performing this research as an academic project for a degree. MJ and our expert were members of the NICE 2010 COPD group. Our respiratory expert has conducted several studies in COPD and has received ex gratia payments for advisory meetings and lectures from Almirall, AstraZeneca, Bayer, Boehringer, Chiesi, GlaxoSmithKline, Nycomed Takeda, Novartis and Pfizer. Our expert’s department has been awarded grants by AstraZeneca, Chiesi, GlaxoSmithKline, etc.

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