Types of studies

We will include randomised controlled trials, including cluster‐randomised trials and quasi‐randomised trials.

We will only include cross‐over trials if data from the first phase are available.

We will only include studies where patients were followed up for at least two weeks.

We will exclude perioperative studies, where the sole purpose of the study was to investigate the effect of oral steroids on surgical outcomes.

Types of participants

Patients with CRS, whether with polyps (CRSwNP) or without polyps (CRSsNP).

We will exclude studies that have 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 will include 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 will be:

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

Other possible comparison pairs include:

• 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 CRS:

• Intranasal steroids versus placebo or no intervention for chronic rhinosinusitis (Chong 2015b).

• Different types of intranasal steroids for chronic rhinosinusitis (Chong 2015a). This review will compare different classes, doses and delivery methods of intranasal corticosteroids for CRS.

• Short‐course oral steroids alone for chronic rhinosinusitis (Chong 2015d). This review will compare 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 will compare oral steroids where they have been used as add‐on therapy to other treatments for CRS (such as intranasal corticosteroids, antibiotics or saline solution).

• Saline irrigation for chronic rhinosinusitis (Chong 2015e). This review will compare nasal saline irrigation for CRS with both placebo/no intervention and with intranasal corticosteroids or antibiotics.

• Systemic and topical antibiotics for chronic rhinosinusitis (Chong 2015c). This review will compare 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 will analyse the following outcomes in the review, but we will 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 will evaluate 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 will analyse data from the longest time periods.

Electronic searches

Published, unpublished and ongoing studies will be identified by searching the following databases from their inception:

• the Cochrane Register of Studies ENT Trials Register;

• the Cochrane Central Register of Controlled Trials (CENTRAL, current issue);

• Ovid MEDLINE (1946 to date);

• Ovid MEDLINE (In‐Process & Other Non‐Indexed Citations);

• PubMed (as a top up to searches in Ovid MEDLINE);

• Ovid EMBASE (1974 to date);

• ClinicalTrials.gov, www.clinicaltrials.gov (search via the Cochrane Register of Studies to date);

• ICTRP (search to date);

• Google Scholar (search to date).

The subject strategies for databases will be modelled on the search strategy designed for CENTRAL (Appendix 1). Where appropriate, these will be 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)).

Searching other resources

We will scan the reference lists of identified publications for additional trials and contact trial authors if necessary. In addition, the Trials Search Co‐ordinator will search PubMed, TRIPdatabase and The Cochrane Library to retrieve existing systematic reviews relevant to this systematic review, so that we can scan their reference lists for additional trials. We will search for conference abstracts using the Cochrane ENT Trials Register and EMBASE.

Selection of studies

At least two review authors will independently screen all titles and abstracts of the studies obtained from the database searches to identify potentially relevant studies. At least two review authors will evaluate the full text of each potentially relevant study to determine if it meets the inclusion and exclusion criteria for this review.

We will resolve any 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 will independently extract data from each study using a standardised data collection form (see Appendix 2). Whenever a study has more than one publication, we will retrieve all publications to ensure complete extraction of data. Where there are discrepancies in the data extracted by different review authors, we will check these against the original reports and resolve differences by discussion and consensus, with the involvement of a third author or a methodologist where appropriate. We will contact the original study authors for clarification or for missing data whenever possible. If differences are found between publications of a study, we will contact the original authors for clarification. We will use data from the main paper(s) if no further information is found.

We will include 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 will also collect baseline information on prognostic factors or effect modifiers. For this review, this includes:

• 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 will extract the findings of the studies on an available case analysis basis; i.e. we will include 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 will extract 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 are not available, we will extract the values for change from baseline. We will analyse 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 appear to be approximately normally distributed or if the analysis that the investigators performed suggests parametric tests were appropriate, then we will treat the outcome measures as continuous data. Alternatively, if data are available, we may convert into binary data.

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

Assessment of risk of bias in included studies

Two review authors will independently assess the risk of bias of each included study. We will follow the guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011) and we will use the Cochrane 'Risk of bias' tool. With this tool we will assess 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

We will summarise the effects of dichotomous outcomes (e.g. proportion of patients with symptom resolution) as risk ratios (RR) with CIs. For the key outcomes that we will present in the 'Summary of findings' table, we will also express the results as absolute numbers based on the pooled results and compared to the assumed risk. We may also calculate the number needed to treat to benefit (NNTB) using the pooled results. 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). If a large number of studies are available, and where appropriate, we may also present additional data based on the assumed baseline risk in (c) a low‐risk population and (d) a high‐risk population.

For continuous outcomes, we will express 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 will provide a clinical interpretation of the SMD values.

Unit of analysis issues

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

Dealing with missing data

We will try to contact study authors via email whenever the outcome of interest is not reported, if the methods of the study suggest that the outcome had been measured. We will do the same if not all data required for meta‐analysis have been reported, unless the missing data are standard deviations. If standard deviation data are not available, we will approximate these using the standard estimation methods from P values, standard errors or 95% CIs if these are reported as detailed in the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011). If it is impossible to estimate these, we will contact the study authors.

Apart from imputations for missing standard deviations, we will conduct no other imputations. We will extract and analyse all data using the available case analysis method.

Assessment of heterogeneity

We will assess 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.

We will assess statistical heterogeneity 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 will assess reporting bias as between‐study publication bias and within‐study outcome reporting bias.

Data synthesis

We will conduct all meta‐analyses using Review Manager 5.3 (RevMan 2014). For dichotomous data, we plan to analyse treatment differences as a risk ratio (RR) calculated using the Mantel‐Haenszel methods. We will analyse time‐to‐event data using the generic inverse variance method.

For continuous outcomes, if all the data are from the same scale, we may pool mean values obtained at follow‐up with change outcomes and report this as a MD. However, if the SMD has to be used as an effect measure, we will not pool 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

We will conduct some subgroup analyses regardless of whether statistical heterogeneity is observed, as these are widely suspected to be potential effect modifiers. For this review, this includes:

• phenotype of patients: whether patients have CRSsNP, CRSwNP, a mixed group or the status of polyps is not known or not reported. We will undertake the subgroup analysis as although there appears to be a considerable overlap between the two forms of CRS 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 will present the main analyses of this review according to the subgroups of phenotypes of CRS. We will present all other subgroup analysis results in tables.

When studies have a mixed group of patients, we will analyse the study as one of the subgroups (rather than as a mixed group) if more than 80% of patients belong to one category. For example, if 81% of patients have CRSsNP, we will analyse the study as that subgroup.

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

• patient age (children versus adults);

• dose;

• duration of treatment.

Sensitivity analysis

We will carry 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 plan 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 will investigate the impact of including data where the validity of the measurement is unclear.

If any of these investigations finds a difference in the size of the effect or heterogeneity, we will mention this in the 'Effects of interventions' section.