Types of studies

We included studies with the following design characteristics:

• randomised controlled trials, including cluster‐randomised trials and quasi‐randomised trials (cross‐over trials were only to be included if the data from the first phase were available); and

• patients were followed up for at least two weeks.

We excluded studies with the following design characteristics:

• randomised patients by side of nose (within‐patient controlled) because it is difficult to ensure that the effects of any of the interventions considered can be localised; or

• perioperative studies, where the sole purpose of the study was to investigate the effect of the intervention on surgical outcome.

Types of participants

Patients with chronic rhinosinusitis, whether with polyps or without polyps.

We excluded studies that included a majority of patients with:

• cystic fibrosis;

• allergic fungal sinusitis/eosinophilic fungal/mucinous rhinosinusitis;

• aspirin‐exacerbated respiratory disease;

• antrochoanal polyps (benign polyps originating from the mucosa of the maxillary sinus);

• malignant polyps;

• primary ciliary dyskinesia;

• gross immunodeficiency (congenital or acquired);

• a history of surgery for nasal polyps within six weeks of entry to the study.

Types of interventions

We included all short (see below) courses of oral steroids, regardless of dose. This includes:

• prednisone;

• prednisolone;

• methylprednisolone;

• hydrocortisone;

• cortisone acetate.

Short courses of oral steroids are defined as lasting up to, but not exceeding, 21 days.

The main comparators were:

• oral steroids plus intranasal corticosteroids versus placebo or no treatment plus intranasal corticosteroids.

Other possible comparison pairs included:

• oral steroid plus co‐intervention X versus placebo/no treatment plus co‐intervention X ('co‐intervention X' refers to any of the other possible co‐interventions).

This review is part of a larger series of six reviews for the treatment of chronic rhinosinusitis:

• Intranasal steroids versus placebo or no intervention for chronic rhinosinusitis (Chong 2016b).

• Different types of intranasal steroids for chronic rhinosinusitis (Chong 2016a). This review compares different classes, doses and delivery methods of intranasal corticosteroids for chronic rhinosinusitis.

• Short‐course oral steroids alone for chronic rhinosinusitis (Head 2016a). This review compares short‐course oral steroids alone with placebo or no intervention, or against other pharmacological interventions such as antibiotics or nasal saline irrigation.

• Short‐course oral steroids as an adjunct therapy for chronic rhinosinusitis (this review). This review compares oral steroids where they have been used as add‐on therapy to other treatments for chronic rhinosinusitis (such as intranasal corticosteroids, antibiotics or saline solution).

• Saline irrigation for chronic rhinosinusitis (Chong 2016c). This review compares nasal saline irrigation for chronic rhinosinusitis with both placebo/no intervention and with intranasal corticosteroids or antibiotics.

• Systemic and topical antibiotics for chronic rhinosinusitis (Head 2016b). This review compares both topical and systemic antibiotics with placebo/no treatment, two different antibiotics with each other and antibiotics with intranasal corticosteroids.

Types of outcome measures

We analysed the following outcomes in the review, but we did not use them as a basis for including or excluding studies.

Both short‐term (at the end of treatment) and long‐term effects are important, therefore we evaluated outcomes at the end of treatment or within three weeks thereof in addition to three to six months, six to 12 months and more than 12 months. For adverse events, we analysed data from the longest time periods.

Electronic searches

The Information Specialist searched:

• the Cochrane Register of Studies ENT Trials Register (searched 11 August 2015);

• the Cochrane Central Register of Controlled Trials (CENTRAL 2015, Issue 7);

• Ovid MEDLINE (1946 to July week 5 2015);

  • Ovid MEDLINE (In‐Process & Other Non‐Indexed Citations) (searched 11 August 2015);

  • PubMed (as a top up to searches in Ovid MEDLINE) (searched 11 August 2015);

• Ovid EMBASE (1974 to 2015 week 32);

• ClinicalTrials.gov, www.clinicaltrials.gov (search via the Cochrane Register of Studies) (searched 11 August 2015);

• World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (searched 11 August 2015);

• Google Scholar (searched 11 August 2015).

The Information Specialist modelled subject strategies for databases on the search strategy designed for CENTRAL. Where appropriate, they were combined with subject strategy adaptations of the highly sensitive search strategy designed by Cochrane for identifying randomised controlled trials and controlled clinical trials (as described in the Cochrane Handbook for Systematic Reviews of Interventions Version 5.1.0, Box 6.4.b. (Handbook 2011). Search strategies for major databases including CENTRAL are provided in Appendix 1.

Searching other resources

We scanned the reference lists of identified publications for additional trials and contacted trial authors where necessary. In addition, the Information Specialist searched PubMed, The Cochrane Library and Google to retrieve existing systematic reviews relevant to this systematic review, so that we could scan their reference lists for additional trials.

Selection of studies

Two review authors independently screened all titles and abstracts of the studies obtained from the database searches to identify potentially relevant studies. The same two review authors evaluated the full text of each potentially relevant study to determine if it met the inclusion and exclusion criteria for this review.

We resolved differences by discussion and consensus, with the involvement of a third author for clinical and/methodological input where necessary.

Data extraction and management

Two review authors independently extracted data from each study using a standardised data collection form (see Appendix 2). If we had found a study that had more than one publication, we would have aimed to retrieve all publications to ensure complete extraction of data. Where there were discrepancies in the data extracted by different review authors, we checked these against the original reports and resolved differences by discussion and consensus, with the involvement of a third author or a methodologist where appropriate. We would have contacted the original study authors for clarification or for missing data whenever needed. If differences had have been found between publications of a study, we would have contacted the original authors for clarification. We would have used data from the main paper(s) if no further information was found.

We included key characteristics of the studies, such as study design, setting, sample size, population and how outcomes were defined or collected in the studies. In addition, we also collected baseline information on prognostic factors or effect modifiers. For this review, these included:

• presence or absence of nasal polyps;

• baseline nasal polyp score (where appropriate);

• whether the patient has had previous sinus surgery;

• number of previous courses of oral steroids.

For the outcomes of interest to the review, we extracted the findings of the studies on an available case analysis basis; i.e. we included data from all patients available at the time points based on the treatment randomised whenever possible, irrespective of compliance or whether patients had received the treatment as planned.

In addition to extracting pre‐specified information about study characteristics and aspects of methodology relevant to risk of bias, we extracted the following summary statistics for each trial and each outcome:

• For continuous data: the mean values, standard deviations and number of patients for each treatment group. Where endpoint data were not available, we extracted the values for change from baseline. We analysed data from measurement scales such as SNOT‐22 and EQ‐5D as continuous data.

• For binary data: the numbers of participants experiencing an event and the number of patients assessed at the time point.

• For ordinal scale data: if the data appeared to be approximately normally distributed or if the analysis that the investigators performed suggested parametric tests were appropriate, then we treated the outcome measures as continuous data. Alternatively, if data were available, we converted into binary data.

We prespecified the time points of interest for the outcomes in this review. While studies may report data at multiple time points, we only extracted the longest available data within the time points of interest. For example, for 'medium‐term' follow‐up periods, our time point is defined as 'three to six months' post‐randomisation. If a study reported data at three, four and six months, we only extracted and analysed the data for the six‐month follow‐up.

Assessment of risk of bias in included studies

Two review authors independently assessed the risk of bias of each included study. We followed the guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011), and we used the Cochrane 'Risk of bias' tool. With this tool we assessed the risk of bias as 'low', 'high' or 'unclear' for each of the following six domains:

• sequence generation;

• allocation concealment;

• blinding of participants, personnel and outcome assessment;

• incomplete outcome data;

• selective reporting;

• other sources of bias.

Measures of treatment effect

If dichotomous outcomes were found, we would have summarised the effects (e.g. proportion of patients with symptom resolution) as risk ratios (RR) with CIs. For the key outcomes that we presented in the 'Summary of findings' table, we would have also expressed the results as absolute numbers and compared to the assumed risk. The assumed baseline risk is typically either (a) the median of the risks of the control groups in the included studies, this being used to represent a 'medium‐risk population' or, alternatively, (b) the average risk of the control groups in the included studies is used as the 'study population' (Handbook 2011).

For continuous outcomes, we expressed treatment effects as a mean difference (MD) with standard deviation (SD) or as standardised mean difference (SMD) if different scales have been used to measure the same outcome. We provided a clinical interpretation of the SMD values.

Unit of analysis issues

This review did not use data from phase II of cross‐over studies or from studies where the patient was not the unit of randomisation, i.e. studies where the side (right versus left) was randomised.

If we had found cluster‐randomised trials, we would have analysed these according to the methods in section 16.3.3 of the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011).

Dealing with missing data

We would have tried to contact study authors via email whenever the outcome of interest was not reported, if the methods of the study had suggested that the outcome had been measured, or where data presented in the paper were in graphical format, in order to try to obtain the study values for the study results. We would have done the same if not all data required for meta‐analysis were reported, unless the missing data were standard deviations. If standard deviation data were not available, we would have approximated these using the standard estimation methods from P values, standard errors or 95% CIs if these were reported as detailed in the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011). If it was impossible to estimate these, we would have contacted the study authors. Apart from imputations for missing standard deviations, no other imputations were planned. However, we had to carry out calculations relating to disease severity (reported as symptom scores) as most of the data were not measured using validated instruments nor reported in a way that was comparable across studies (see 'Imputing total symptom scores' below).

We extracted and analysed all data using the available case analysis method.

Assessment of heterogeneity

If we had found more than one study for each of the comparisons, we would have assessed clinical heterogeneity (which may be present even in the absence of statistical heterogeneity) by examining the included trials for potential differences between studies in the types of participants recruited, interventions or controls used and the outcomes measured.

If heterogeneity had been detected we would have assessed it by visually inspecting the forest plots and by considering the Chi² test (with a significance level set at P value < 0.10) and the I² statistic, which calculates the percentage of variability that is due to heterogeneity rather than chance, with I² values over 50% suggesting substantial heterogeneity (Handbook 2011).

Assessment of reporting biases

We assessed reporting bias as between‐study publication bias and within‐study outcome reporting bias.

Data synthesis

If we had found more than one study in within a comparison pair, we would have conducted all meta‐analyses using Review Manager 5.3 (RevMan 2014). If we had found dichotomous data, we would have analysed treatment differences as a risk ratio (RR) calculated using the Mantel‐Haenszel methods. We would have analysed time‐to‐event data using the generic inverse variance method.

For continuous outcomes, if we had found that data were from the same scale, we might have pooled mean values obtained at follow‐up with change outcomes and reported this as a MD. However, if the SMD had to be used as an effect measure, we would not have pooled change and endpoint data.

When statistical heterogeneity is low, random‐effects versus fixed‐effect methods yield trivial differences in treatment effects. However, when statistical heterogeneity is high, the random‐effects method provides a more conservative estimate of the difference.

Subgroup analysis and investigation of heterogeneity

Had we found more than one study for each comparison pair, we would have conducted the following subgroup analyses regardless of whether statistical heterogeneity was observed, as these are widely suspected to be potential effect modifiers:

• whether patients had chronic rhinosinusitis without nasal polyps, chronic rhinosinusitis with nasal polyps, were a mixed group or the status of polyps is not known or not reported.

We would have undertaken the subgroup analysis as although there appears to be a considerable overlap between the two forms of chronic rhinosinusitis with regards to inflammatory profile, clinical presentation and effect of treatment (Cho 2012; DeMarcantonio 2011; Ebbens 2010; Fokkens 2007; Ragab 2004; Ragab 2010; van Drunen 2009), there is some evidence pointing to differences in the respective inflammatory profiles (Kern 2008; Keswani 2012; Tan 2011; Tomassen 2011; Zhang 2008; Zhang 2009), and potentially even differences in treatment outcome (Ebbens 2011).

We would have presented the main analyses of this review according to the subgroups of phenotypes of chronic rhinosinusitis. We would have presented all other subgroup analysis results in tables.

None of the studies had a mixed group of patients. If a mixed group of patients had been found within the paper, we would have analysed the study as one of the subgroups (rather than as a mixed group) if more than 80% of patients had belonged to one category.

In addition to the subgroups above, we had planned to conduct the following subgroup analyses in the presence of statistical heterogeneity:

• patient age (children versus adults);

• dose;

• duration of treatment.

Sensitivity analysis

Had we found more than one study for each comparison, we would have carried out sensitivity analyses to determine whether the findings are robust to the decisions made in the course of identifying, screening and analysing the trials. We had planned to conduct sensitivity analysis for the following factors, whenever possible:

• impact of model chosen: fixed‐effect versus random‐effects model;

• risk of bias of included studies: excluding studies with high risk of bias (we define these as studies that have a high risk of allocation concealment bias and a high risk of attrition bias (overall loss to follow‐up of 20%, differential follow‐up observed);

• how outcomes were measured: we would have investigated the impact of including data where the validity of the measurement is unclear.

If any of these investigations had found a difference in the size of the effect or heterogeneity, we would have mentioned this in the Effects of interventions section.