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Hypertonic saline (HS) for acute bronchiolitis: Systematic review and meta-analysis
© Maguire et al. 2015
Received: 25 June 2015
Accepted: 10 November 2015
Published: 23 November 2015
Acute bronchiolitis is the commonest cause of hospitalisation in infancy. Currently management consists of supportive care and oxygen. A Cochrane review concluded that, “nebulised 3 % saline may significantly reduce the length of hospital stay”. We conducted a systematic review of controlled trials of nebulised hypertonic saline (HS) for infants hospitalised with primary acute bronchiolitis.
Searches to January 2015 involved: Cochrane Central Register of Controlled Trials; Ovid MEDLINE; Embase; Google Scholar; Web of Science; and, a variety of trials registers. We hand searched Chest, Paediatrics and Journal of Paediatrics on 14 January 2015. Reference lists of eligible trial publications were checked. Randomised or quasi-randomised trials which compared HS versus either normal saline (+/− adjunct treatment) or no treatment were included. Eligible studies involved children less than 2 years old hospitalised due to the first episode of acute bronchiolitis. Two reviewers extracted data to calculate mean differences (MD) and 95 % Confidence Intervals (CIs) for length of hospital stay (LoS—primary outcome), Clinical Severity Score (CSS) and Serious Adverse Events (SAEs). Meta-analysis was undertaken using a fixed effect model, supplemented with additional sensitivity analyses. We investigated statistical heterogeneity using I2. Risk of bias, within and between studies, was assessed using the Cochrane tool, an outcome reporting bias checklist and a funnel plot.
Fifteen trials were included in the systematic review (n = 1922), HS reduced mean LoS by 0.36, (95 % CI 0.50 to 0.22) days, but with considerable heterogeneity (I2 = 78 %) and sensitivity to alternative analysis methods. A reduction in CSS was observed where assessed [n = 516; MD −1.36, CI −1.52, −1.20]. One trial reported one possible intervention related SAE, no other studies described intervention related SAEs.
There is disparity between the overall combined effect on LoS as compared with the negative results from the largest and most precise trials. Together with high levels of heterogeneity, this means that neither individual trials nor pooled estimates provide a firm evidence-base for routine use of HS in inpatient acute bronchiolitis.
Acute bronchiolitis is the most common cause for hospitalisation in infancy and childhood, with 1–3 % of all infants admitted to hospital during their first winter [1–9]. Obstruction of the airways results in severe breathing difficulties caused by common respiratory viruses infecting the lungs [1–8, 10–13]. The peak age of incidence is between 1 and 6 months for babies admitted with this condition . Current management involves supportive care, minimal handling, supplemental oxygen and fluids [4, 14–16]. The median duration of admission is 3 days, considerably higher than for other acute paediatric admissions (median 1 day). The course of the illness or length of hospital stay has not been impacted by treatments including oral and inhaled steroids, antiviral agents and a variety of bronchodilators.
A number of small studies have suggested that nebulised hypertonic saline may influence the course of the illness resulting in a reduction in the duration of hospitalisation for infants admitted with “acute bronchiolitis” [17–20]. A Cochrane review, which last updated its searches in May 2013, included 11 trials involving 1090 infants with mild to moderate acute viral bronchiolitis (500 inpatients, six trials; 65 outpatients, one trial; and 525 emergency department patients, four trials) . The review concluded that “current evidence suggests nebulized 3 % saline may significantly reduce the length of hospital stay and improve the clinical severity score in infants with acute viral bronchiolitis.” Our team felt that this conclusion is difficult to justify on two counts. Firstly, the findings are hampered by high levels of heterogeneity, and we believe these warrant further exploration. Secondly, a number of relevant published trials, published at the time appear to have been overlooked; this is still the case as of the 2013 update. Finally, since 2013, a number of large studies addressing this topic have been published.
As a result, we made a registration on the PROSPERO database and undertook a separate systematic review on the effect of hypertonic saline on the length of stay of infants admitted to hospital for acute bronchiolitis. The PROSPERO protocol is available (Additional file 1). This review does not investigate the use of hypertonic saline in infants with bronchiolitis in the emergency department.
This study is reported in accordance with the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) guidance . A checklist is available (Additional file 2). Since this study was a literature review of previously reported studies, ethical approval or additional consent from participants was not required.
Protocol and registration
The protocol was registered with the PROSPERO database (CRD42014007569)  on 03 March 14 and the registration was updated on 18 December 2014.
We included published and unpublished randomised controlled trials involving children up to the age of 2 years, hospitalised as the result of a first episode of acute bronchiolitis. Trials were included if hypertonic saline versus either normal saline (+/− adjunct treatment) or no treatment were the interventions. Studies were grouped in pre-specified subgroups as follows: (1) Nebulised hypertonic saline alone vs normal saline; (2) Nebulised hypertonic saline plus a bronchodilator (e.g. salbutamol) vs. normal saline; (3) Nebulised hypertonic saline plus a bronchodilator vs. normal saline plus same bronchodilator; (4) Nebulised hypertonic saline alone or plus a bronchodilator vs. no intervention. We applied no restrictions based on the concentration, dose or administration of the intervention or control. We excluded studies not published in English.
Literature search and information sources
We searched Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE (via Ovid), EMBASE from inception to January 2015, Web of Science from 2010 to January 2015 and Google Scholar. We used 2010 as a cut off, the date on which Zhang and colleagues ran their searches for the 2011 update . We used the terms “bronchiolitis” and “hypertonic saline” to identify ongoing unpublished data in the following registries: Clinicaltrials.gov; UK Clinical Trials Gateway (UKCTG); CRD databases (DARE NHS EED, HTA); controlled-trials.com; centrewatch.com and National Research Register (NNR). On 14th January 2015 we also hand-searched Chest, Paediatrics and Journal of Paediatrics using the terms “hypertonic saline” and “bronchiolitis”. One reviewer (HC) checked the reference lists of all eligible trial publications for other relevant trials. The final search strategy is outlined in Additional file 3.
Two reviewers (CM and HC) independently assessed eligibility, differences were resolved through discussion with third reviewers (DH and ME). Where the titles or abstracts suggested eligibility, we retrieved and screened the full paper. Unsuccessful attempts were made to contact trial investigators of three unpublished studies [25–27] to request additional unreported data.
CM and HC used a standardised data collection tool to include study characteristics, population characteristics and risk of bias . Population and study data comprised of country where the trial was conducted, age, disease severity, intervention and comparator details (concentration, dose, delivery mechanism), and details of any adjunct treatments given (β2 agonist or epinephrine). We extracted baseline and follow-up outcome data for Length of hospital stay (LoS), final Clinical Severity Scores (CSS) using the scoring system described by Wang and colleagues , readmission rate and adverse events. Adverse event data was collected however reported but of particular interest were tachycardia, hypertension, pallor, tremor, nausea, vomiting and acute urinary retention. DH helped resolve any discrepancies with any of the data items.
Risk of bias
We separately assessed the potential for systematic error within individual studies using the Cochrane risk of bias tool  and the following dimensions of methodological quality: (1) generation of allocation sequence; (2) allocation concealment; (3) blinding (participant and researchers); (4) blinding of outcome assessors; (5) completeness of outcome data; (6) selective outcome reporting. Studies were grade as being at, “low”, “high” or “unclear” risk of bias. Any discrepancies were discussed between the data extractors until both reached a unanimous decision. Where an unclear grading was given we contacted trial authors to obtain further information and searched for the study protocol to identify sources of reporting bias. We used standard methods (based on the Cochrane Handbook) to assess funnel plot symmetry as we had greater than 10 trials in the meta-analysis . We employed methods suggested by Dwan and colleagues  to assess the risk of outcome reporting bias for each of the outcomes using the Outcome Reporting Bias (ORB) classification whereby trials are scored as “high risk”, “low risk” or “partial risk”. The full classification table is available in Additional file 4.
The primary outcome was LoS. Secondary outcomes were adverse events, final CSS scores and rate of readmission. Data on LoS and final mean CSS was used to calculate mean differences (MD) with 95 % Confidence Intervals (CIs) for each outcome. Where trials included arms using different concentrations of hypertonic saline in addition to a control arm we treated them as two separate trials, dividing the control arm numbers by two in order not to double-count control participants. Meta-analyses were undertaken in RevMan Version 5.2 and Stata version12 using both fixed (Inverse-Variance) and random effect (Der Simonian & Laird) models ; additional sensitivity analyses used the metasens package as implemented within the R software version 3.1.3. The four pre-specified intervention subgroups were separated in the main forest plot to give subgroup estimates of treatment effects. Statistical heterogeneity—a measure of within-trial variation—was investigated using the I2 statistic : 0–40 % indicating unimportant levels; 30–60 % showing moderate heterogeneity; 50–100 % as demonstrable heterogeneity within trials. Sensitivity analyses were undertaken as proposed by Deschartres et al.  along with meta-regression to assess whether heterogeneity could be attributed to measurable sources. An assessment for the potential of publication bias was made via assessment of the funnel plot generated for all trials included in the meta-analysis. We produced a narrative description of adverse events and readmission rates.
Searches and selection
The remaining 18 trials (total number of children included in the analysis) were conducted in: Italy (n = 106) ; United Arab Emirates and Canada (n = 91) ; China (n = 205) [63, 64]; Israel (n = 93) [18, 19]; Argentina (n = 82) ; India (n = 388) [65–67]; Qatar (n = 171) ; Georgia (n = 42) ; The Netherlands (n = 247) ; USA (n = 190) ; Turkey (n = 69) ; Mexico (n = unknown) ; Nepal (n = 59)  and UK (n = 290)  (Additional file 6). The sample size ranged from 40  to 317  participants. Eligibility criteria varied significantly in terms of patient characteristics and disease severity (Additional file 7). The upper age limit for subjects ranged from 12 to 24 months. Amongst the range of clinical characteristics required for inclusion were ‘bronchiolitis with temperature >38 °C’ , ‘first episode of wheezing with evidence of viral infection’ , ‘wheezing’ , ‘wheeze and/or crackles’ , ‘crackles’ , and ‘first episode of bronchiolitis’. In terms of severity, oxygen saturation in air was specified in 4 studies and ranged from <97 to <92 %. Numbers of participants allocated to each group was clearly defined in all but three trials [26, 27, 69] whose data was not usable in the meta-analysis as attempts to contact the author were fruitless.
Length of hospital stay mean (SD) (days)
Final CSS score
Al-Ansari 2010 et al. 
Intervention (3 % HS): 3.84 (2.84)
Intervention (3 % HS): F19 M39
Moderate to severe
Intervention (3 % HS): 1.4 (1.41)
Intervention (5 % HS): 4.02 (2.56)
Intervention (5 % HS): F26 M31
Intervention (5 % HS): 1.56 (1.38)
Control: 3.30 (2.43)
Control: F26 M31
Control: 1.88 (1.76)
Espelt et al. 2012 
Intervention: F24 M26
Intervention: 5.8 (2.7)
Control: F26 M24
Control: 5.47 (2.1)
Everard et al. 2014 
Intervention: 3.3 (2.6)
Intervention: F69 M73
Intervention: 4.19 (3.20)
Control: 3.4 (2.8)
Control: F64 M85
Control: 4.22 (3.52)
Giudice et al. 2012 
Intervention: 4.8 (2.3)
Intervention: F18 M34
Intervention: 4.9 (1.3)
Intervention: 6.5 (1.6)
Control: 4.2 (1.6)
Control: 5.6 (1.6)
Control: 7.7 (1.6)
Kuzik et al. 2007 
Intervention: 4.4 (3.7)
Intervention: F20 M27
Intervention: 2.6 (1.9)
Control: 4.6 (4.7)
Control: F19 M30
Control: 3.5 (2.9)
Luo et al. 2010 
Intervention: 6.0 (4.3)
Intervention: 6 (1.2)
Intervention: 1.5 (0.5)
Control: 5.6 (4.5)
Control: 7.4 (1.5)
Control: 2.9 (0.7)
Luo et al. 2011 
Intervention: 5.9 (4.1)
Moderate to severe
Intervention: 4.8 (1.2)
Intervention: 1.7 (0.6)
Control: 5.8 (4.3)
Control: 6.4 (1.4)
Control: 3.1 (0.7)
Maheshkumar et al. 2013 
Mild to moderate
Intervention: 2.25 (0.89)
Control: 2.88 (1.76)
Mandelberg et al. 2003 
Intervention: 3 (1.2)
Intervention: F12 M15
Intervention: 3 (1.2)
Control: 2.6 (1.9)
Control: F9 M15
Control: 4 (1.9)
Nemsadze et al. 2013 
Mild to moderate
Intervention: 4.4 (1.1)
Control: 4.9 (1.2)
Ojha et al. 2014 
Intervention: 8.61 (5.74)
Intervention: 1.87 (0.96)
Control: 8.51 (4.24)
Control: 1.82 (1.18)
Ozdogan et al. 2014 
Overall: 7.1 (5.48)
Mild to moderate
Pandit et al. 2013 
Moderate to severe
Intervention: 3.92 (1.72)
Control: 4.08 (1.90)
Sharma et al. 2013 
Intervention: 4.93 (4.31)
Intervention: F28 M97
Intervention: 2.64 (0.88)
Control: 4.18 (4.24)
Control: F31 M92
Control: 2.66 (0.93)
Silver et al. 2014 
Intervention: 3.86 (3.01)
Intervention (3%HS): F31 M62
Intervention: 2.49 (1.64)
Control: 4.39 (2.95)
Control: F37 M60
Control: 2.47 (1.76)
Sosa-Bustamante et al. 2014 
Moderate to severe
Tal et al. 2006 
Intervention: 2.8 (1.2)
Intervention: F11 M10
Intervention: 2.6 (1.4)
Intervention: 5.35 (1.3)
Control: F7 M13
Control: 3.5 (1.7)
Control: 6.45 (1)
Teunissen et al. 2014 
Intervention (3 % HS): 3.6 (5.2)
Intervention (3 % HS): F40 M44
Mild to moderate
Intervention (3 % HS): 3.43 (2.24)
Intervention (3 % HS): 3.87 (3.15)
Intervention (6 % HS): 3.4 (3.8)
Intervention (6 % HS): F35 M48
Intervention (6 % HS): 3.74 (2.99)
Intervention (6 % HS): 5.16 (4.20)
Control: 3.6 (5.0)
Control: F31 M49
Control: 2.82 (2.25)
All trials administered 3 % hypertonic saline via a nebuliser as the active intervention; three trials were designed with an additional arm using higher concentrations of hypertonic saline at 5 % [27, 68] or 6 % . Fifteen of the eighteen trials stated the amount of hypertonic saline administered which ranged from 3 ml [25, 67] to 4 ml [18–20, 26, 63–66, 70–73] or in one trial 5 ml . Four trials compared hypertonic saline versus normal saline alone [20, 64, 71, 72] or versus standard care  with no additional treatments. Where the flow rate was stated (n = 10) it ranged between 5 and 10 L/min [18, 19, 62, 65–68, 70, 71, 73]. Investigators in the other trials administered different adjunct treatments alongside hypertonic saline: five trials administered epinephrine/adrenaline [18, 19, 62, 66, 68]; seven administered a β2 agonist (salbutamol, albuterol) [25–27, 63, 65, 67, 70]; one trial did not specify any additional medication  and five trials did not administer different adjunct treatments alongside hypertonic saline [20, 64, 71–73].
The majority of trials stated that they administered 0.9 % of normal saline as the control group except one where “oxygen therapy plus best supportive care” was the control  or where authors did not state the concentration of normal saline [67, 69]. Eight of the trials gave oxygen therapy in both the intervention and control arms [20, 62, 64, 65, 67, 68, 70, 73], nine trials did not specify whether oxygen therapy was provided [18, 19, 25–27, 63, 69, 71, 72] and one trial stated oxygen therapy was provided in the intervention arm but did not state whether this was provided in the control arm . The flow rate of the nebulisers in the control groups matched those in the intervention arm of each trial.
Risk of bias
We graded two of these as being at high risk of bias: one provided no explanation regarding the uneven distribution of withdrawals  and one did not state which arms the 16 patients were excluded from . The median loss to-follow-up at the time of the primary outcome assessment (LoS) was 8 % (range 0 % [20, 63, 66, 67] to 18 % [25, 72]; twelve studies did not complete an intention to treat analysis, presenting instead an ‘available case analysis’ for only those participants for whom a LoS could be identified [18–20, 25, 62, 64, 65, 68, 70–73]. Three studies completed a full analysis on all participants randomised [63, 66, 67].
Results and synthesis
Five trials contributed to the mean difference in final CSS scores (n = 516, MD −1.36 (95 % CI −1.52 to −1.20); we observed no statistical heterogeneity [19, 62–64, 70]. One trial reported one SAE possibly related to the intervention , no other studies described intervention related SAE’s.
In an analysis of three studies that reported readmission rate [68, 71, 73] (651 participants), no difference was observed between hypertonic saline and control [RR 0.90, 95 % CI 0.52 to 1.55]; there was no statistical heterogeneity (I2 = 0 %). A decision was made not to attempt a meta-analysis of adverse event data which, where reported, was mainly narrative and not consistently captured across trials. We present a narrative summary in Additional file 9. One study described one SAE, of bradycardia and desaturation during administration of the nebuliser, which had resolved by the following day , no other studies described any serious adverse events related to the intervention of hypertonic saline.
Summary of findings
Summary of findings table
Relative effect (95 % CI)
No of Participants (studies)
Quality of the evidence (GRADE)
Normal saline (+/− adjunct treatment) or oxygen therapy plus best supportive care
Hypertonic saline (+/− adjunct treatment)
Hypertonic saline versus normal saline alone (days)
The mean length of hospital stay ranged across control groups from 1.82 to 6.4 days
The mean length of hospital stay ranged across hypertonic saline groups from 1.87 to 4.8 days
0.58 (95 % CI −0.86 to −0.30) days
452 (4 inpatient trials)
⊕ ⊕ ⊕ ⊕ higha
Hypertonic saline plus B2 agonist vs normal saline plus B2 agonist (days)
The mean length of hospital stay ranged across control groups from 2.66 to 7.4 days
The mean length of hospital stay ranged across hypertonic saline groups from 2.25 to 6 days
0.18 (95 % CI −0.36 to 0.01 days)
710 (5 inpatient trials)
⊕ ⊕ ⊕⊖ moderateb
Hypertonic saline plus epinepherine vs normal saline plus epinephrine (days)
The mean length of hospital stay ranged across control groups from 1.88 to 5.6 days
The mean length of hospital stay ranged across hypertonic saline groups from 1.4 to 4.9 days
0.56 (95 % CI −0.86 to −0.27 days)
470 (5 inpatient trials)
⊕ ⊕ ⊕ ⊕ highc
Hypertonic saline alone or plus bronchodilator versus no intervention (days)
The mean length of hospital stay for control groups was 3.7 days
The mean length of hospital stay in the hypertonic saline group was 3.7 days
0.07 (95 % CI −0.61 to 0.27 days)
290 (1 inpatient trial)
⊕ ⊕ ⊕⊖ moderated
Strengths and limitations of the findings
High levels of statistical heterogeneity associated with the meta-analysis dominate the results making their interpretation challenging. The addition of concomitant medications may explain some of this heterogeneity across intervention subgroups, with as the largest effect sizes found in trials where hypertonic saline was given alone. Studies were conducted across a number of different healthcare settings with diverse local services, usual care, guidelines (e.g. definition of “fit to discharge”) and disease severity at entry, all of which must contribute to the extensive intra-trial variation observed. That many of the largest trials contributed such little weight to the analysis undermines our confidence in the results. Furthermore, the absence of re-admission rate in the majority of trials may suggest the intervention is not as economically beneficial as the results suggest.
A key strength is the inclusion of 15 of the 18 trials in the meta-analysis of the primary outcome. This facilitated both investigation of publication bias and allowed for subgroup analyses and aggregate data meta-regression, although there was incomplete data in relation to secondary outcomes and trial design features.
One can argue the potential of publication bias based on the uncharacteristic funnel plot shape. Systematic error is not thought to always be caused by application of language restrictions to meta-analyses despite the potential reduction of the precision of pooled estimates . Nonetheless, restriction of trials to only English articles may have altered the precision, effect size, heterogeneity and overall risk of bias.
Summary of heterogeneity
The definition of ‘acute bronchiolitis’ differs between countries, and indeed across clinicians in the same institution. Inevitably this diversity was reflected in the description of infants included which variously specified wheeze and or crackles (n = 4) [20, 68, 70, 73]; a first episode of wheezing (n = 5) [62–66]; “bronchiolitis” (n = 4) [19, 67, 71, 72]; or bronchiolitis with a temperature >38C (n = 1) ; while information was absent in four others [25–27, 69]. The term “wheeze” is itself open to interpretation (and sometimes misinterpretation) within the medical profession [78–82], and may be taken to include children presenting with their first exacerbation of asthma, and manifesting as bronchospasm. The occurrence of this is less common among younger patients, and as a consequence we may have expected the effect size to vary according to the mean age of the study population. Nevertheless, our meta-regression to investigate this was equivocal.
Variation among discharge criteria
The consistency of the outcomes—specifically ‘length of stay’ and ‘fit for discharge’—is self-evidently defined and assessed in very different ways across the studies. Moustgaard et al. suggest that definition of outcomes in trials is a widespread problem. The studies set (sometimes arbitrary) criteria regarding when the patient stay started, including “from study entry, which was within 12 h of admission” (n = 2) [20, 62]; from hospital admission (n = 3) [65, 68, 73]; or from first dose of study medication (n = 2)[70, 71]; information was absent for the remaining 11 studies [18, 19, 25–27, 63, 64, 66, 67, 69, 72]. The reported time to entry into study varied from 3 to 24 h, and generally did not specify whether “entry” corresponded to consent or first treatment. The latter criterion in particular represents a huge proportion of an admission in units with mean stays of 72 h or less. Similarly, discharge was defined and assessed differently across studies. In one study the discharge assessment used a continuous discharge criteria ,but in at least five others the decision to discharge was made only once a day [18, 19, 63, 65, 66], meaning the time of discharge is effectively a discrete outcome which occurs at intervals of 24 h. Although this inevitably overestimates the real time taken to be fit for discharge, it does so equally for both groups and would be expected to underestimate rather than overestimate the difference between the groups. With this in mind we have no explanation for why the positive studies are based on a once daily clinical assessment.
In the remaining studies the frequency of assessment for discharge was unclear. We present a summary of the discharge criteria in Additional file 10.
Publication, generalisability and other biases
This difference in practice may also, in large part, explain the differences in observed treatment effects in the large UK, Dutch and USA studies which found no benefit as compared with the apparently large effect observed in other studies [70, 71, 73]. While early indications of a potential benefit may have been attributable to publication bias [86, 87] the positive effects of later large studies may be attributable to study design and cultural effects. It is of note that all the recent studies of hypertonic saline have failed to demonstrate any benefit yet the ‘meta-analysis still appears to favour the treatment. This effect is largely driven by the relatively large studies of Luo et al. and it is likely that this is explicable when considering discharge criteria in more detail (see above).
In summary therefore, there remains considerable heterogeneity which are not germane to being captured and quantified by standard meta-regression tools. Clearly, a large amount of the heterogeneity is driven by two trials from the same team, led by Luo [63, 64], with outlying results, relatively small sample sizes but narrow confidence intervals (around a day, compared with a day-and-a-half in SABRE  and the other large northern European study—Teunissen 2014 ). The removal of these two studies from the main analysis considerably reduces the effect sizes and statistical significance in the analyses to a more modest (and minimal) impact. Nevertheless, this does not eliminate heterogeneity completely.
Finally, there choice whether to favour a fixed- or random-effects analysis remains open to debate, with strong and apparently compelling proponents on both sides [32, 88–91]. The presence of unexplained heterogeneity goes against the assumption of a single underlying (fixed) effect, and this is commonly taken to justify the random effect model. When the heterogeneity is excessive however, the random effect model has the unfortunate operational characteristic of allocating similar weights to all trials, irrespective of their size and precision. Our decision to pre-specify a fixed-effect as the primary analysis was taken to counter this limitation. That said, we are unable to offer a clinically sensible reason why the largest trial should be allocated only 4 % of the weight in this analysis. Given this, together with the large and unexplained heterogeneity in general, our recommendation is that no single overall summary measure—fixed, random or otherwise—is an adequate reflection of the identified trials. Although we investigated response in relation to dose (3, 5 or 6 %), the studies did not provide data on frequency or duration of HS, which may also have varied across studies.
Strengths and limitations compared to other reviews
Building on the review conducted by Zhang and colleagues which contained 11 RCTs (n = 1090), our review included 15 trials (n = 1922) which included three much larger trials which unanimously showed null results [65, 70, 73]. We limited our inclusion criteria to trials of inpatient infants, whereas Zhang et al. also included outpatient and emergency department trials. Al-Ansari has been included in our review despite being included in the emergency department group by Zhang and colleagues, as the length of stay infers that the patients were admitted . Despite this, our meta-analysis included a further 8 trials [25, 65–67, 70–73] which altogether unearthed significantly higher levels of heterogeneity than that stated in the previous Cochrane review. A potential explanation is that we applied no restrictions in terms of dose or way the intervention was administered, and in addition we included data from one unpublished study: Zhang et al. made no statement in regards to these.
Duplication is not without merit—it enables the replicability of methods to be demonstrated, as well as adding weight to or disputing the current evidence base [92–94]. Even when faced with identical data, approaches taken and interpretations made can differ between researchers . A well-defined rationale for any such duplicate review, as required by the PRISMA checklist (though not explicitly) , provides transparency regarding overlaps and subsequently, allows for informed debate about its value to the evidence base .
Implications for policy and practice
The disparities between the results of the largest, most precise trials and all the included trials, together with high levels of heterogeneity, mean that neither individual trials nor pooled estimates provide a firm evidence-base for the use of hypertonic saline in inpatient acute bronchiolitis . The refutation of initially large treatment effects in small trials by larger trials stronger is a phenomenon which is observed more widely and should not surprise the reader . For instance, in the treatment of acute bronchiolitis, initial evidence supporting the use of β2-agonists has also been overturned as successive trials have been published .
Our aggregate level data analysis was unable to identify specific settings and characteristics which influence the effect of HS on LoS. Systematic sensitivity analyses, ideally based on individual patient data and regression analyses are warranted to better understand why hypertonic saline showed substantial benefit in some trials yet none in others . In the absence of this, there is no robust evidence to support the use of hypertonic saline.
Claims that hypertonic saline achieves small reductions in LoS must be treated with scepticism based on the 15 known trials of HS. The findings appear at best highly dependent on trial design and local policies. We cannot rule out the possibility that inhaled HS offers symptomatic relief but have no data to support or deny this possibility.
No specific funding supported the initial work on this review, however revisions to the work were undertaken during the write-up of the Hypertonic Saline in Acute Bronchiolitis: Randomised Controlled Trial and Economic Evaluation (SABRE). This project was funded by the Health Technology Assessment programme (HTA 09/91/22) and will be published in full in the Health Technology Assessment journal series. Further information available at: http://www.nets.nihr.ac.uk/projects/hta/099122. This report presents independent research commissioned by the NIHR. The views and opinions expressed by authors in this publication are those of the authors and do not necessarily reflect those of the NHS, the NIHR, MRC, CCF, NETSCC, the Health Technology Assessment programme or the Department of Health. The Authors gratefully acknowledge the contribution of unpublished data by Bettina Loza of the VieCuri Medisch Centrum voor Noord Limburg, Venlo, The Netherlands and Alyssa Silver of The Children’s Hospital of Montefiore, Bronx, New York.
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