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Cochrane Database of Systematic Reviews Protocol - Intervention

Saline irrigation for chronic rhinosinusitis

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Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To evaluate the effects of saline irrigation in patients with CRS.

Background

Description of the condition

Chronic rhinosinusitis (CRS) represents a common source of ill health; 11% of UK adults reported CRS symptoms in a worldwide population study (Hastan 2011). Symptoms, including nasal obstruction, nasal discharge, facial pain, anosmia and sleep disturbance, have a major impact on quality of life, reportedly greater in several domains of the SF‐36 than angina or chronic respiratory disease (Gliklich 1995). Acute exacerbations, inadequate symptom control and respiratory disease exacerbation are common. Complications are rare, but may include visual impairment and intracranial infection.

Two major phenotypes of CRS have been identified based on the presence or absence of nasal polyps on examination. Nasal polyps are tumour‐like hyperplastic swellings of the nasal mucosa, most commonly originating from within the ostiomeatal complex (Larsen 2004). Chronic rhinosinusitis with nasal polyps (CRSwNP) is diagnosed when polyps are seen (on direct or endoscopic examination) bilaterally in the middle meatus. The acronym CRSsNP is used for the condition in which no polyps are present.

Although the aetiology of CRS is not fully understood, it may involve abnormalities in the host response to irritants, commensal and pathogenic organisms and allergens, obstruction of sinus drainage pathways, abnormalities of normal mucociliary function, loss of the normal mucosal barrier or infection. Two typical profiles may be observed with respect to inflammatory mediators; in eosinophilic CRS, which is typically associated with nasal polyps, high levels of eosinophils, immunoglobulin E (IgE) and interleukin (IL)‐5 may be found, while in neutrophilic CRS, more often associated with CRS without polyps, neutrophils predominate, with elevated interferon (IFN) gamma, IL‐8 and tumour necrosis factor (TNF).

Despite the differences in phenotype and aetiology, in clinical practice many treatments for CRS are initiated without knowledge of a patient's 'polyp status'. Even when it is known whether or not a patient with CRS has polyps, this knowledge does not always suggest adjustments to treatment. This review (and most of its companion reviews) will consider patients with and without polyps together in the initial evaluation of treatment effects. However, subgroup analyses will explore potential differences between them.

The most commonly used interventions for CRS are used either topically (sprayed into the nose) or systemically (by mouth) and include steroids, antibiotics and saline.

Description of the intervention

Nasal irrigation (also know as nasal douche, wash or lavage) is a procedure that rinses the nasal cavity with water, or isotonic or hypertonic saline solutions. Nasal irrigation with saline (salt water) is common to both modern and traditional therapy regimes. Delivered by bottle, spray, pump or nebuliser, the topical use of saline has been included as a supplement to most treatment protocols.

How the intervention might work

The physiological mechanisms underlying any benefit of the use of saline are difficult to define but many theories exist. It is commonly proposed that mechanical clearance of mucus is the sole basis of its effect (saline thins mucus and helps to clear it out). However, there is an increasing perception that saline has a contributory role in the resolution of inflammation and does not just relieve symptoms for mechanical reasons. Other theories include improvement in the clearance of mucus (which is also a potential medium for bacterial growth), enhanced ciliary beat activity, removal of antigen, biofilm or inflammatory mediators and a protective role in the sinonasal mucosa (Brown 2004). Both the methods of delivery and tonicity of saline irrigation are therefore postulated as possible factors that affect its efficacy.

Why it is important to do this review

Nasal saline irrigation is commonly used as a treatment for CRS. The treatment has been widely adopted based on the presumption that it does not do patients any harm and it is cheap and widely available. This is an update of a Cochrane review that assessed its effectiveness (Harvey 2007). We will evaluate the optimal method of delivery and whether other concentrations of sodium chloride (than found in normal saline) are as effective. We will seek to establish the role of nasal saline irrigation in three ways: by assessing i) its benefits or harms by comparing it against no treatment or 'placebo', ii) its relative effects when compared to other treatments for CRS, and iii) its role as an add‐on therapy for patients who are already using other treatments, such as intranasal corticosteroids.

This review is one of a suite of reviews looking at management options for patients with CRS (Chong 2015a; Chong 2015b; Chong 2015c; Chong 2015d; Chong 2015e). Unlike previous Cochrane reviews, and other published systematic reviews, these reviews will specifically focus on clinically relevant treatment regimes and outcomes. We will not include studies designed to evaluate interventions in the immediate peri‐surgical period, which are focused on improving the surgical procedure or post‐surgical results.

Objectives

To evaluate the effects of saline irrigation in patients with CRS.

Methods

Criteria for considering studies for this review

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 exclude studies that randomised patients by side of nose (within‐patient controlled). It is difficult to ensure that the effects of any of the interventions considered can be localised.

We will only include studies where patients were followed up for at least three months, to reflect the importance of focusing on long‐term outcomes for a chronic condition.

We will exclude perioperative studies, where the sole purpose of the study was to investigate the effect of saline 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;

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

Types of interventions

Saline, as an active treatment, delivered to the nose by any means (douche, irrigation, drops, spray or nebuliser, using an intermittent, continuous or pulsed strategy).

The comparators will be: no treatment or placebo or other standard treatments such as intranasal corticosteroids.

The main comparison pairs are:

  • nasal saline versus no treatment/placebo;

  • nasal saline plus intranasal corticosteroids versus placebo or no treatment plus intranasal corticosteroids.

Other possible comparison pairs include:

  • nasal saline versus intranasal corticosteroids;

  • nasal saline type A versus other types/delivery methods/volumes of nasal irrigation;

  • hypertonic versus isotonic saline.

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 2015a).

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

  • Short‐course oral steroids alone for chronic rhinosinusitis (Chong 2015c). 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 (Chong 2015d). 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 (this review). 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 2015e). 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.

Primary outcomes

  • Health‐related quality of life, using disease‐specific health‐related quality of life scores, such as the Sino‐Nasal Outcome Test‐22 (SNOT‐22), Rhinosinusitis Outcome Measures‐31 (RSOM‐31) and SNOT‐20.

  • Disease severity, as measured by patient‐reported symptom score (such as the Chronic Sinusitis Survey (CSS) questionnaire and visual analogue scales).

  • Significant adverse effect: epistaxis.

Secondary outcomes

  • Health‐related quality of life, using generic quality of life scores, such as the SF‐36, EQ‐5D and other well‐validated instruments.

  • Other adverse effects: local irritation.

  • Other adverse effects: discomfort.

  • Endoscopic score (depending on population, either nasal polyps size score or endoscopy score, e.g. Lund Mackay).

  • Computerised tomography (CT) scan score (e.g. Lund Kennedy).

Outcomes will be measured at 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.

Search methods for identification of studies

The Cochrane ENT Trials Search Co‐ordinator will conduct systematic searches for randomised controlled trials and controlled clinical trials. There will be no language, publication year or publication status restrictions. We may contact original authors for clarification and further data if trial reports are unclear and we will arrange translations of papers where necessary.

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.

Data collection and analysis

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 polyps score;

  • whether the patient has had previous sinus surgery.

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.

Outcome reporting bias (within‐study reporting bias)

We will assess within‐study reporting bias by comparing the outcomes reported in the published report against the study protocol, whenever this can be obtained. If the protocol is not available, we will compare the outcomes reported to those listed in the methods section. If results are mentioned but not reported adequately in a way that allows analysis (e.g. the report only mentions whether the results were statistically significant or not), bias in a meta‐analysis is likely to occur. We will seek further information from the study authors. If no further information can be found, we will note this as being a 'high' risk of bias. Quite often there will be insufficient information to judge the risk of bias; we will note this as an 'unclear' risk of bias (Handbook 2011).

Publication bias (between‐study reporting bias)

We will assess funnel plots if sufficient trials (more than 10) are available for an outcome. If we observe asymmetry of the funnel plot, we will conduct more formal investigation using the methods proposed by Egger 1997.

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 this 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 that points 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). Sinus penetration of irrigation fluids differs in patients with and without polyps, and according to whether previous sinus surgery has been conducted (Brown 2004).

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 (volume or frequency);

  • tonicity;

  • duration of treatment;

  • method of delivery.

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.

GRADE and 'Summary of findings' table

We will use the GRADE approach to rate the overall quality of evidence using the GDT tool (http://www.guidelinedevelopment.org/) for the main comparison pairs listed in the Types of interventions section. The quality of evidence reflects the extent to which we are confident that an estimate of effect is correct and we will apply this in the interpretation of results. There are four possible ratings: 'high', 'moderate', 'low' and 'very low'. A rating of 'high' quality evidence implies that we are confident in our estimate of effect and that further research is very unlikely to change our confidence in the estimate of effect. A rating of 'very low' quality implies that any estimate of effect obtained is very uncertain.

The GRADE approach rates evidence from RCTs that do not have serious limitations as high quality. However, several factors can lead to the downgrading of the evidence to moderate, low or very low. The degree of downgrading is determined by the seriousness of these factors:

  • study limitations (risk of bias);

  • inconsistency;

  • indirectness of evidence;

  • imprecision;

  • publication bias.

The 'Summary of findings' table will present only the seven top priority outcomes (disease‐specific HRQL, disease severity score, adverse effects and generic quality of life score). We will not include the outcomes of endoscopic score and CT scan score in the 'Summary of findings' table.