Colutorios, enjuagues bucales y aerosoles para mejorar la recuperación después de la amigdalectomía
Resumen
Antecedentes
Esta es una actualización de una revisión Cochrane publicada por primera vez en The Cochrane Library , número 1, 2010 y actualizada previamente en 2011.
La amigdalectomía es la extirpación quirúrgica de la amígdala palatina, constituida por tejido linfático y ubicada en la parte posterior de la faringe. Esta intervención aún se realiza con frecuencia en pacientes que tienen episodios recurrentes de amigdalitis aguda. Aunque la amigdalectomía se considera un procedimiento bastante menor, el dolor y la hemorragia son dos de las complicaciones más frecuentes; cualquiera de ellas puede retrasar la recuperación y en ocasiones, puede llevar al reingreso hospitalario. La medicación posterior a la amigdalectomía debe proporcionar una reducción adecuada de la morbilidad y al mismo tiempo, reducir los efectos secundarios, por lo que los agentes tópicos parecen ser una opción segura e ideal. Se encuentran disponibles varios enjuagues bucales y aerosoles tópicos que proporcionan alivio del dolor o que pueden ayudar a reducir la hemorragia en el período posoperatorio inmediato.
Objetivos
Evaluar los efectos de los colutorios, los enjuagues bucales y los aerosoles en la mejoría de la recuperación posterior a la amigdalectomía.
Métodos de búsqueda
Se realizaron búsquedas en el registro de ensayos del Grupo Cochrane de Enfermedades de Oído, Nariz y Garganta (Cochrane Ear, Nose and Throat Disorders Group); en el Registro Cochrane Central de Ensayos Controlados (Cochrane Central Register of Controlled Trials, CENTRAL); en PubMed; en EMBASE; en CINAHL; en Web of Science; en Cambridge Scientific Abstracts; en ICTRP y en fuentes adicionales de ensayos publicados y no publicados. La fecha de la búsqueda más reciente fue el 4 de julio de 2013.
Criterios de selección
Se incluyeron ensayos controlados aleatorizados en los que se compararon los colutorios, los enjuagues bucales y los aerosoles, utilizados antes y después de la operación, con placebo en adultos o niños sometidos a amigdalectomía, con o sin adenoidectomía.
Obtención y análisis de los datos
Dos autores de la revisión seleccionaron los ensayos para la inclusión, evaluaron el riesgo de sesgo y extrajeron los datos de forma independiente.
Resultados principales
Se incluyeron siete ensayos (593 participantes; 397 niños y 196 adultos). El período de seguimiento varió entre 24 horas y dos semanas. Algunos ensayos proporcionaron datos confiables para los resultados primarios preestablecidos y ninguno para los resultados secundarios. El riesgo de sesgo fue alto en la mayoría de los ensayos incluidos. El aerosol de lidocaína pareció ser más efectivo que el aerosol de solución salina para la reducción de la gravedad del dolor hasta el tercer día posoperatorio. Un escaso número de participantes tuvo una sensación de ardor o de escozor con el aerosol de bencidamina, pero no tan intensa como para suspender el uso.
Conclusiones de los autores
La escasa calidad de la información y los datos inadecuados no permitieron llegar a conclusiones amplias y fiables. Los ensayos futuros se deben realizar de forma adecuada y prestar más atención a los métodos utilizados para evaluar los resultados, el momento adecuado de las evaluaciones y la calidad del informe y el análisis posterior de los datos.
PICO
Resumen en términos sencillos
Colutorios, enjuagues bucales y aerosoles para mejorar los resultados después de la amigdalectomía
La amigdalectomía es una de las cirugías más frecuentes que se realizan en adultos y niños. El dolor y la hemorragia después de la operación son comunes. La medicación posoperatoria de la amigdalectomía debe intentar disminuir algunos de estos síntomas. Se encuentran disponibles varios colutorios y aerosoles tópicos que proporcionan alivio del dolor o que pueden ayudar a reducir la hemorragia en el período inmediatamente posterior a la cirugía.
Esta revisión incluyó siete estudios con 593 participantes (397 niños y 196 adultos) y está actualizada hasta julio de 2013. El riesgo de sesgo fue alto en la mayoría de los ensayos incluidos. Se encontró que el aerosol de lidocaína parecía ser más efectivo que un aerosol salino de placebo para reducir la gravedad del dolor hasta el tercer día postoperatorio. Un pequeño número de participantes tuvo una sensación de ardor o escozor cuando utilizó otro aerosol que contenía bencidamina, pero no fue tan intensa como para suspender su uso.
Las investigaciones futuras deben proporcionar evidencia confiable para que los pacientes puedan tomar decisiones informadas sobre la efectividad de estos tratamientos para la reducción de los síntomas y complicaciones más frecuentes posteriores a la amigdalectomía.
Authors' conclusions
Summary of findings
| Oral rinses, mouthwashes and sprays to improve recovery after tonsillectomy | ||||||
| Patient or population: patients with tonsillectomy | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | No of participants | Quality of the evidence | Comments | |
| Assumed risk | Corresponding risk | |||||
| Control | Lidocaine | |||||
| Pain: severity score day 1 | The mean pain severity score on day 1 in the control groups was | The mean pain severity score on day 1 in the intervention groups was | 40 | ⊕⊕⊝⊝ | ||
| *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). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1The incompleteness of trial details, and in particular the lack of clarity about sequence generation and concealment, was a serious limitation in the included trial (Kaygusuz 2003). Subjective outcome assessment of pain coupled with potentially inadequate blinding leading to biased assessment of the intervention effect are likely to have further compromised the quality of the evidence. | ||||||
Background
Description of the condition
This is an update of a Cochrane review first published in The Cochrane Library in Issue 1, 2010 and previously updated in 2011.
Tonsillectomy is the surgical removal of lymphoid tissue, the palatine tonsil, which is located at the back of the throat. Although a Cochrane review (Burton 2009) highlighted some uncertainty regarding the indications for tonsillectomy and its effectiveness in terms of the benefits and relative risks, it is still commonly performed for patients who have recurrent bouts of acute tonsillitis. The National Prospective Tonsillectomy Audit (NPTA) in the UK reported that 76% of patients who underwent tonsillectomy did so due to recurrent acute tonsillitis (Ramsden 2005). However, as a result of increased usage of antibiotics in the management of tonsillitis there has been a recent shift in the indications for tonsillectomy in paediatric patients, from the treatment of infection (recurrent acute tonsillitis) to the treatment of airway obstruction (obstructive sleep apnoea) (Lim 2001), although chronic infection remains the most common indication for adult tonsillectomy (Hoddeson 2008).
A range of surgical techniques continue to be used; these include 'cold' cutting, dissection and snaring, electrocautery, laser tonsil ablation (LTA), harmonic (ultrasonic) scalpel (Burton 2004), monopolar radiofrequency ablation, bipolar radiofrequency ablation (coblation) (Burton 2007), thermal welding and micro‐debriding.
Despite the fact that tonsillectomy is considered a fairly minor procedure, it is often associated with significant postoperative morbidity including pain, bleeding, difficulty in swallowing, earache, fever, mouth odour, weight loss and reduced oral intake (Mann 1999). Pain and bleeding are two of the most common complications; either may delay recovery and can lead to hospital readmission (Chacra 2005; Lee 1996; Schloss 1994).
Postoperative pain, ranging from mild to severe, may last from a few days to two weeks and can affect oral intake, sleeping pattern and ultimately the quality of life (Chacra 2005). Severe pain has been reported in 20% to 50% of children and young adults who have undergone tonsillectomy (Canbay 2008; Kotiniemi 1997; Romsing 2000). A Cochrane systematic review found that there was no evidence that perioperative use of local anaesthetic injection and local anaesthetic spray could improve postoperative pain control (Hollis 1999).
Post‐tonsillectomy primary or reactive bleeding rates (within the first 24 hours) can vary from 0.3% to 2.1%, whilst the rate of secondary bleeding requiring admission to hospital varies from 2% to 10% (Lee 2004; Ramsden 2005; Raut 2001; Walker 2007). Although neither a Cochrane review (Pinder 2011) nor a more recent literature review (Leinbach 2003) identified any difference in the rate of secondary haemorrhage after a range of surgical techniques, there have been reports more recently of lower bleeding rates after 'cold' tonsillectomy techniques when compared with 'hot' tonsillectomy techniques (Walker 2007).
Description of the intervention
The ideal postoperative tonsillectomy medication should provide an adequate reduction in morbidity while minimising side effects, therefore topical agents would seem to be an ideal, safe option. There are a number of mouthwashes and topical sprays available which offer pain relief or may be able to help reduce postoperative bleeding.
How the intervention might work
Surgical tissue damage is responsible for a substantial proportion of the pain and bleeding following tonsillectomy. Some mouthwashes have a direct mode of action by either anaesthetising the area, providing topical pain relief (analgesic effect) (e.g. lidocaine hydrochloride aerosol (Grainger 2008)) or both.
It is also suggested that post‐tonsillectomy morbidity may in part be due to an increase in the colonisation of bacteria on the tonsillar bed and its subsequent inflammation. Therefore oral rinses which are capable of decreasing this microbiological colonisation and inflammation (e.g. hydrogen peroxide, topical antibiotics and corticosteroids) could also be indirectly effective in controlling postoperative pain (Chacra 2005) and bleeding (Pai 2005).
Why it is important to do this review
A number of topical agents, oral rinses and mouthwashes have been used in the management of acute post‐tonsillectomy pain and bleeding. Some of these agents (e.g. hydrogen peroxide (H2O2) mouth rinses) have been used for many years. Interventions to improve recovery following tonsillectomy have been evaluated in a number of studies, but to the best of our knowledge there has not been a systematic review of the evidence for the effectiveness of oral rinses, mouthwashes and sprays.
Objectives
To assess the effects of oral rinses, mouthwashes and sprays for improving recovery following tonsillectomy.
Methods
Criteria for considering studies for this review
Types of studies
Randomised controlled trials (RCTs).
Types of participants
Adults and children without significant comorbidity (e.g. diabetes, chronic lung disease, bleeding disorders), who underwent tonsillectomy, with or without adenoidectomy, by any of the recognised surgical techniques.
Types of interventions
We considered studies in which oral rinses, mouthwashes and sprays, used pre‐ and postoperatively, have been compared with placebo for the outcomes sought in this review.
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Oral rinses and mouthwashes used as a rinse or gargle preoperatively and postoperatively.
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Spraying of any topically acting agent onto the surgical site postoperatively.
We excluded 'swish and swallow' agents with potential systemic effects which might confound assessment of the primary outcomes sought for this review. Concomitant administration of any other form of pain medication which may influence any of the outcomes was acceptable providing it was available equally to both the treatment and control group.
Types of outcome measures
We included any of the following outcomes, evaluated at the time of discharge, during the first 48 hours and at any time points in follow‐up for a period of two months postoperatively.
Primary outcomes
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Pain: reduction in severity.
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Pain: time to complete resolution.
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Pain medication: postoperative pain medication type, dosage and reduction in the demand postoperatively.
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Bleeding: time to complete cessation.
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Bleeding: postoperative measures to reduce bleeding.
Secondary outcomes
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Readmission for any reason.
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Duration of hospital stay.
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Time to return to normal diet and activities.
Adverse outcomes
We reported on any specific adverse effects, systemic or local toxicity, any clinically diagnosed hypersensitivity or other unacceptable or adverse events associated with any of these treatments.
Search methods for identification of studies
We conducted systematic searches for randomised controlled trials. There were no language, publication year or publication status restrictions. We were unsuccessful in obtaining clarification of trial details from trial investigators but managed to arrange translations of papers not in the English language. The date of the last search was 4 July 2013, following previous searches in 2011 and 2009.
Electronic searches
We searched the following databases from their inception: the Cochrane Ear, Nose and Throat Disorders Group Trials Register; the Cochrane Central Register of Controlled Trials (CENTRAL, The Cochrane Library 2013, Issue 6); PubMed; EMBASE; CINAHL; LILACS; KoreaMed; IndMed; PakMediNet; CAB Abstracts; Web of Science; ICTRP; Clinicaltrials.gov; ISRCTN; Google Scholar and Google. In searches prior to 2013, we also searched BIOSIS Previews 1926 to 2011.
We modelled subject strategies for databases on the search strategy designed for CENTRAL. Where appropriate, we combined subject strategies with adaptations of the highly sensitive search strategy designed by The Cochrane Collaboration for identifying randomised controlled trials and controlled clinical trials (as described in theCochrane Handbook for Systematic Reviews of Interventions Version 5.1.0, Box 6.4.b. (Higgins 2011). Search strategies for major databases including CENTRAL are provided in Appendix 1.
Searching other resources
We scanned reference lists of identified publications for additional trials and made attempts to contact trial investigators by e‐mail to ask for details of additional published and unpublished trials. We searched PubMed, TRIPdatabase, Google and DynaMed to retrieve existing systematic reviews possibly relevant to this review, and scanned their reference lists for additional trials.
Data collection and analysis
Selection of studies
For this update four review authors (Zbys Fedorowicz (ZF), Esther van Zuuren (EVZ), Mona Nasser (MN) and Jassim H Al Langawi (JHL) independently assessed the abstracts of studies resulting from the searches. We obtained full copies of all relevant and potentially relevant studies, those appearing to meet the inclusion criteria, and those for which there were insufficient data in the title and abstract to make a clear decision. Zbys Fedorowicz (ZF) and Esther van Zuuren (EVZ) independently assessed the full‐text papers and resolved any disagreement on the eligibility of retrieved studies through discussion and consensus, or through a third party (Mona Nasser (MN)). We excluded all irrelevant records and noted details of the studies and the reasons for their exclusion in the Characteristics of excluded studies table in RevMan 5.2 (RevMan 2012).
Data extraction and management
We entered study details into the Characteristics of included studies table in RevMan 5.2. The review authors collected outcomes data using a pre‐determined form designed for this purpose.
In the previous updates two review authors entered extracted data into RevMan 5.2 and only included data if there was an independently reached consensus. Any disagreements were resolved by consulting with a third review author.
We extracted the following details.
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Trial methods: (a) method of allocation, (b) masking of participants, trialists and outcomes assessors, (c) exclusion of participants after randomisation and proportion and reasons for losses at follow‐up.
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Participants: (a) country of origin and location: private clinic or academic institute, (b) sample size, (c) age, (d) sex, (e) inclusion and exclusion criteria.
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Intervention: (a) type, dosage, (b) length of time in follow‐up.
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Control: (a) type, dosage, (b) length of time in follow‐up.
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Outcomes: (a) primary and secondary outcomes mentioned in the Types of outcome measures section of this review.
If stated, we recorded the sources of funding of any of the included studies. We used this information to help us to assess heterogeneity and the external validity of the trials.
Assessment of risk of bias in included studies
Three review authors (ZF, EVZ and MN) assessed the risk of bias of the selected studies independently using The Cochrane Collaboration's tool for assessing risk of bias as described in Chapter 8, section 8.5, of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We compared the evaluations and discussed and resolved any disagreements between the review authors.
We assessed the following domains as 'low risk of bias', 'unclear' (uncertain risk of bias) or 'high risk of bias':
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sequence generation;
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allocation concealment;
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blinding (of participants, personnel and outcome assessors);
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incomplete outcome data;
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selective outcome reporting;
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other bias.
These assessments are reported for each individual study in the 'Risk of bias' tables (Characteristics of included studies).
Measures of treatment effect
Reduction in pain severity
Where this was reported as a discrete outcome, it had been measured with either a standardised visual analogue scale (VAS) (continuous data) or with a short categorical scale (ordinal data). We did not dichotomise these continuous data but calculated and presented the mean difference (MD) and 95% CI in pain severity between intervention and placebo groups.
We were unable to exercise the option to dichotomise the categorical outcomes data reported in the included studies because the ordinal data were only presented as mean daily scores and the reports did not provide sufficient independent data for further analysis. These data were not reported in this review.
Pain medication usage
Pain medication was reported as means per day for the treatment groups in one study.
Unit of analysis issues
Only studies with a parallel‐group design were included, so participants had been randomised to either intervention or control with subsequent analysis at individual allocation level.
Dealing with missing data
We made attempts to retrieve missing data from some of the investigators in the included trials but in view of the age of some of these trials this proved unsuccessful.
Assessment of heterogeneity
In view of the lack of data that could be included in a meta‐analysis we did not assess clinical heterogeneity, but in future updates or if further data are available we will apply the following methods of assessment:
We will assess clinical heterogeneity by examining the characteristics of studies, the similarity between types of participants and the interventions. We plan to report heterogeneity as important if it is substantial (I2 statistic value between 50% and 90%, Higgins 2011); if the I2 statistic is greater than 90%, a meta‐analysis will not be carried out. However, if heterogeneity could be explained by clinical reasoning and a coherent argument could be made for combining the studies, we will enter these into a meta‐analysis.
Assessment of reporting biases
The paucity of trials and lack of data reporting the effects of the interventions did not permit an assessment of publication bias. In future updates we will assess publication bias by following the recommendations on testing for funnel plot asymmetry as described in section 10.4.3.1 of the Cochrane Handbook for Systematic Reviews of Interventions 5.1.0 (Higgins 2011), and this will be explored in the Discussion if appropriate.
Data synthesis
We sought statistical advice from the Cochrane ENT Group. Two review authors (MN and ZF) analysed data which addressed the primary and secondary outcomes of this review and had been extracted from the included studies using RevMan 5.2 (RevMan 2012) and reported analyses as suggested in Chapter 9 of the Cochrane Handbook for Systematic Reviews of Interventions 5.1.0 (Higgins 2011).
We did not attempt to synthesise the extracted data but in future updates or if further data become available the following methods will apply.
For the synthesis and meta‐analysis of any quantitative data we will use the fixed‐effect and random‐effects models as appropriate. If we establish that there is significant heterogeneity between the trials, we will use the random‐effects model.
In the event that there are insufficient clinically homogeneous trials for any specific intervention or insufficient study data that can be pooled, we will present a narrative synthesis.
Subgroup analysis and investigation of heterogeneity
Lack of data did not permit a subgroup analysis but in future updates and if further data become available the following methods will apply.
We will conduct a subgroup analysis by splitting and categorising the data based on the type of mouth rinse, its method of action and its use either pre‐ and/or postoperatively. We will also compare and analyse relevant outcomes data in which differing tonsillectomy procedures have been utilised in any of the included trials. We will explore the effects of confounding in the assessment of postoperative pain in studies where participants have undergone tonsillectomy alone or combined with adenoidectomy if an appropriate number of trials are found.
Sensitivity analysis
The limited amount of data extracted from the included studies did not permit a sensitivity analysis. For future updates and if there are sufficient included studies we plan to conduct sensitivity analyses to assess the robustness of our review results by repeating the analysis with the following adjustments: exclusion of studies with unclear or inadequate allocation concealment, unclear or inadequate blinding of outcomes assessment and unclear or inadequate completeness of follow‐up.
Results
Description of studies
See: Characteristics of included studies and Characteristics of excluded studies.
Results of the search
The initial search in 2009 retrieved 70 references to studies. After examination of the titles and abstracts of these references, all but 27 studies were eliminated and excluded from further evaluation. We obtained full‐text copies of the remaining studies, four of which required translation (Giacomelli 1984; Rustamov 1978; Schlorhaufer 1965; Schmidtmayer 1981). The review authors discussed the eligibility of these remaining studies, resolved any uncertainties by consensus and finally excluded all but six studies, which met our inclusion criteria.
The searches were re‐run on 22 April 2011 and retrieved eight references to studies, none of which were eligible for inclusion in this review.
The latest search was conducted on 4 July 2013 and provided an additional 42 references to studies. After examination of the titles and abstracts all but seven were excluded. We obtained the full text of two reports and accessed the protocols to five ongoing studies; we subjected these to further evaluation. No further eligible studies other than one ongoing study were identified for inclusion (see Characteristics of ongoing studies). One previously excluded study (Schmidtmayer 1981) was reassessed and included in the review.
For further details of the search history see Figure 1.
Study flow diagram.
Included studies
Seven studies, all of which were randomised, double‐blinded, placebo‐controlled trials, were included in this review (Abou Chacra 2005; Giacomelli 1984; Kaygusuz 2003; Raj 1986; Schmidtmayer 1981; Valijan 1989; Young 1987).
None of the included studies comprehensively addressed the primary and secondary outcomes specified in the protocol for this review and they only provided a limited amount of reliable data. However, we considered that the inclusion of these studies and the reporting of their results would help provide at least some evidence towards answering this research question.
Characteristics of the trial setting and investigators
The trials were conducted in the ENT departments of university or general hospitals in Turkey (Kaygusuz 2003), the UK (Raj 1986; Valijan 1989; Young 1987), Canada (Abou Chacra 2005), Germany (Schmidtmayer 1981) and Italy (Giacomelli 1984). They took place over different time periods ranging from 24 hours to up to two weeks (Abou Chacra 2005) postoperatively.
The providers of treatment in the trials were university and hospital research staff and the assessors of outcomes included the healthcare providers, ancillary staff, the participants and their carers.
Characteristics of the participants
The total sample size comprised 593 participants (397 children, 196 adults). Gender was incompletely reported in several of the studies. Two separate age groups, adults (14 to 62 years) and children (four to eight years), were studied in Raj 1986, only adults participated in Schmidtmayer 1981 and Valijan 1989, and the participants in the four remaining studies consisted of children and adolescents. Participants in all of the included studies had been previously admitted for elective tonsillectomy with or without adenoidectomy and were generally discharged either the same day or within 48 hours.
Interventions
In all of the trials, with the exception of Abou Chacra 2005 in which participants used mouth rinses and in Schmidtmayer 1981 gargles, the interventions were delivered by sprays (Giacomelli 1984; Kaygusuz 2003; Raj 1986; Valijan 1989; Young 1987).
Benzydamine hydrochloride was the most frequently used intervention (Giacomelli 1984; Raj 1986; Schmidtmayer 1981; Valijan 1989; Young 1987), whilst lidocaine was used in Kaygusuz 2003 and hydrogen peroxide in Abou Chacra 2005.
These interventions were compared with normal saline spray (Kaygusuz 2003), water (Abou Chacra 2005; Valijan 1989) and an unspecified placebo (Giacomelli 1984; Raj 1986; Schmidtmayer 1981; Young 1987).
The exact timing and duration of administration of the interventions varied markedly between the studies. In Abou Chacra 2005, Giacomelli 1984, Kaygusuz 2003, Schmidtmayer 1981, Valijan 1989 and Young 1987 participants received the interventions at varying times postoperatively. In Raj 1986 they were delivered once intra‐operatively and for an unspecified time postoperatively. In those studies in which the intervention was administered after the immediate postoperative period it was either self administered, by a nurse or by the participant's parent or carer.
Outcomes
The severity of postoperative pain, which was one of the primary outcomes of this review, was assessed in all of the studies with the exception of Schmidtmayer 1981, but there was wide variability between the studies in terms of the methods used, the timing of the assessments, the assessors of these outcomes and the quality of reporting and subsequent analysis of the data.
These outcomes were assessed with a standardised visual analogue scale (VAS) in Abou Chacra 2005, Kaygusuz 2003 and Valijan 1989, and by ordinal rating scales in Giacomelli 1984, Raj 1986 and Young 1987. They were self assessed in Kaygusuz 2003 and Valijan 1989, and investigator‐assessed in Young 1987. In the remaining studies, with the exception of Giacomelli 1984 in which it was unclear who the assessors were, the assessments were made by the investigators, carers and participants.
In two of the studies (Valijan 1989; Young 1987) the methods used to assess outcomes and the corresponding data were inadequately reported.
The only study that addressed the use of postoperative pain medication, dosage and reduction in demand postoperatively was Schmidtmayer 1981.
The daily pain scores in one study (Giacomelli 1984) were collected from a short (four‐point) categorical symptom scale, and were transformed into mean daily scores. However, the averaging of ordinal data obtained from the narrow range of possible answers on this type of scale into means and mean change scores is generally considered incapable of providing a value that is readily interpretable or particularly useful.
In several of the studies the pain ratings were not reported separately but the data were consolidated into composite global symptom scores.
The rather limited data in Raj 1986 were only reported as global symptom scores which included ratings for sore throat, dysphagia and earache.
The investigators in Kaygusuz 2003 reported that a VAS was used to assess severity of pain "caused by drinking 100 ml of water" but the report was unclear if this stimulus was applied at any of the assessment times other than the immediate postoperative period (< 24 hours).
Although none of the included studies reported any appreciable data related to postoperative bleeding, all of the included studies, other than Giacomelli 1984, Kaygusuz 2003 and Young 1987, reported some data on analgesic usage, but most of these data were not suitable for further analysis.
None of the secondary outcomes specified in the protocol for this review were addressed by the included studies. Ultimately the outcome assessments reported in the included studies provided a limited amount of useful data.
Further details are available in the Characteristics of included studies table.
Excluded studies
All of the studies which were excluded from this review and the reasons for their exclusion are listed in the Characteristics of excluded studies table.
Risk of bias in included studies
We categorised risk of bias in the included studies according to the following:
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low risk of bias (plausible bias unlikely to seriously alter the results) if all criteria were met;
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moderate risk of bias (plausible bias that raises some doubt about the results) if one or more criteria were partly met; or
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high risk of bias (plausible bias that seriously weakens confidence in the results) if one or more criteria were not met.
We classified the majority of the included studies as 'high risk of bias', an assessment which was to a certain extent based on the inadequate reporting of the criteria that are a prerequisite in the evaluation of methodological rigour in terms of trial design and conduct. Concealment of the allocation sequence and blinding are key domains in the assessment of risk of bias and more especially where studies include subjective outcomes assessments.
For further details see the 'Risk of bias' graph (Figure 2) and 'Risk of bias' summary (Figure 3).
'Risk of bias' graph: review authors' judgements about each methodological quality item presented as percentages across all included studies.
'Risk of bias' summary: review authors' judgements about each methodological quality item for each included study.
Allocation
Randomisation
The method of randomisation was not clearly reported in any of the studies and therefore we judged this domain as 'unclear' for all of these studies.
Allocation concealment
Inadequate reporting quality, emphasised by a degree of uncertainty as to whether adequate measures had been taken to ensure that the investigators were unaware of the upcoming assignment, did not permit a clear judgement of the risk of bias for this domain in all of the included studies, other than Abou Chacra 2005 which we judged as high risk of bias.
Blinding
Unfortunately the inconsistent and less than satisfactory quality of reporting did not enable clear, accurate and complete judgements to be made for the adequacy of blinding of the healthcare providers, participants or assessors of the outcomes in most of the included studies.
The investigators in one study (Abou Chacra 2005) indicated that although the solutions were in identical bottles the participants were able to recognise the difference in taste between the intervention and control.
The reportedly "identical characteristics" of the preparations used in Giacomelli 1984 would appear to confirm that the participants were effectively blinded but the report was unclear as to how the investigators were blinded to the interventions allocated to the participants.
In Kaygusuz 2003 the interventions were initially administered intraoperatively and although the blinding of the participants appears to have been effective for this time period the report was unclear how blinding was further ensured in the postoperative administration period. This report also did not describe how the investigators were blinded to the assigned interventions.
Effective blinding of both the participants and investigators in Raj 1986 and Valijan 1989 was achieved by the use of a placebo and active preparation which were similar in taste, smell and colour.
Although the investigators in Schmidtmayer 1981 and Young 1987 stated that their study was double‐blind, it was not possible to make a clear judgement about this domain based on the information presented in the report.
The satisfactory and effective blinding of outcome assessors in Abou Chacra 2005, Giacomelli 1984, Kaygusuz 2003, Schmidtmayer 1981 and Young 1987 could not be confirmed from the study details presented in these reports.
Incomplete outcome data
There was no evidence of incomplete reporting of outcome data in two of the studies (Raj 1986; Schmidtmayer 1981) but in Giacomelli 1984, Kaygusuz 2003, Valijan 1989 and Young 1987 it was 'unclear'. There were substantial losses to follow‐up in Abou Chacra 2005; the outcome data were incompletely reported and losses were inadequately addressed and therefore we judged this domain as high risk of bias in this study.
Selective reporting
Although the study protocols were not available for any of the studies, five of them (Abou Chacra 2005; Kaygusuz 2003; Raj 1986; Schmidtmayer 1981; Young 1987), based on information available in the respective methods sections, reported on all of the stated objectives and expected outcomes. The report in Giacomelli 1984 was unclear and it was not possible to make a definitive judgement about this item in this review. We also judged the remaining studies as not entirely free of selective reporting for the reasons described in the corresponding 'Risk of bias' table for each study (Characteristics of included studies).
Other potential sources of bias
Whilst it was unclear if the pharmaceutical company sponsorship of three trials (Raj 1986; Valijan 1989; Young 1987) could be deemed a potential source of bias, other potential sources of bias were identified in Abou Chacra 2005 and Schmidtmayer 1981 (see 'Risk of bias' tables).
We considered the two remaining studies (Giacomelli 1984; Kaygusuz 2003) to be free of other potential sources of bias.
Effects of interventions
Due to clinical diversity between the studies in terms of their interventions, the methodological diversity in study design and the overall inadequate standard of reporting of data, it was not possible to synthesise the data and a narrative synthesis is presented.
Pain: reduction in severity, time to complete resolution, analgesic usage
Only one of the included trials provided some reliable data on the reduction of pain severity (Kaygusuz 2003). In this study lidocaine spray appeared to be more effective than NaCl (saline) spray at reducing pain, but the effect was rather limited and lasted only until the third day post‐tonsillectomy (see Analysis 1.1; Analysis 1.2; Analysis 1.3; Figure 4; Figure 5; Figure 6).
Forest plot of comparison: 1 Pain severity, outcome: 1.1 Day 1.
Forest plot of comparison: 1 Pain severity, outcome: 1.2 Day 3.
Forest plot of comparison: 1 Pain severity, outcome: 1.3 Day 7.
Contradictory conclusions reached by the investigators in Giacomelli 1984 and Raj 1986 in terms of the effectiveness of pain relief with benzydamine, and the lack of its effectiveness in Valijan 1989 and Young 1987, could not be supported by the data presented by the investigators in any of these trials.
The mean number of tablets per day (lozenges of acetylsalicylic acid) over seven days was 14.2 in the intervention group versus 19.0 in the placebo group (Schmidtmayer 1981).
The paucity of data and the implausible analysis in Abou Chacra 2005 did not permit reliable conclusions to be reached about postoperative analgesic usage in this trial and therefore the data have not been included in this review. None of the other included trials provided any data for analgesic usage.
Bleeding: time to complete cessation, postoperative measures to reduce bleeding
Only one trial (Abou Chacra 2005) reported on this outcome but provided limited data. Bleeding was reported on the sixth postoperative day and occurred only in the group that received hydrogen peroxide. However, the measures, if any, that were used to reduce the bleeding were unstated.
Readmission for any reason, duration of hospital stay
No data were available.
Time to return to normal diet and activities
None of the studies reported data on these outcomes.
Adverse outcomes
A small number of participants experienced a burning sensation with benzydamine in Raj 1986 and a stinging sensation in Valijan 1989, but it was stated that this was not sufficient for them to discontinue usage. No other adverse effects were reported in the remaining trials.
Discussion
Summary of main results
Our comprehensive search for randomised controlled trials which examined the effects of the interventions specified in the protocol for this review retrieved a number of trials in which the investigators appeared to be supportive of the effectiveness of several interventions, but provided very limited and poor‐quality data to substantiate these claims. We were unable to obtain adequate data from most of the trials and we summarise only the results from our analysis of two of the outcomes from two of the trials.
Pain severity when lidocaine was used as a topical spray was markedly less (P < 0.05) when compared with 9% NaCl (saline) spray in the immediate and up to three days post‐tonsillectomy period, but the results in both groups were not dissimilar by the seventh day (Kaygusuz 2003).
Overall completeness and applicability of evidence
It was quite striking to see how few of the included trials, a number of which date back 20 years, although apparently addressing post‐tonsillectomy morbidity, have provided such limited and incomplete evidence for the effect of sprays and mouthwashes in improving postoperative outcomes for such a common surgical procedure.
Conceivably the use of more potent and possibly longer‐acting systemic rather than topical analgesics might be considered more appropriate for pain relief and in particular if their use might obviate the necessity of repetitive and possibly painful spraying of a raw surgical area, notwithstanding the attendant problems of compliance, particularly in the child or younger patient.
Whilst the applicability of evidence of the benefits of topically acting agents such as lidocaine in providing some measure of analgesia is perhaps not in question, this may not be the case with the rather limited, if any, topical analgesic properties of either benzydamine or hydrogen peroxide. However, the applicability of the perceived benefits of lidocaine may need to be offset by the possible inconvenience of having to spray the surgical site several times a day for a number of days.
Pain is not the only post‐tonsillectomy sequela and, although the complexities involved in assessing pain are acknowledged, the evaluation of the recognised anti‐inflammatory properties of benzydamine and in particular its effects on accelerating the healing process would have been a valuable contribution to the overall completeness of the evidence base.
Quality of the evidence
We were unable to provide a 'Summary of findings' (SoF) table to assess the quality of evidence across all the studies and therefore provide a descriptive summary of the assessment for only one primary outcome from a single study (Kaygusuz 2003) from which the relevant data were available.
Pain: reduction in severity, time to complete resolution
Limitations in study design
The lack of clarity in sequence generation and its concealment, in addition to inadequate blinding coupled with potentially biased assessment of the effects of the intervention, are likely to have compromised the quality of the evidence.
Unexplained heterogeneity and inconsistency of results
As only one trial was included in summary of findings Table for the main comparison this assessment was not applicable.
Indirectness of evidence (indirect population, intervention or control, outcomes)
Although the included trial met the eligibility criteria for inclusion it only addressed a restricted version of the review in terms of this outcome, in not providing any data for the time to complete resolution of pain which is an important patient preferred outcome for this review question.
Imprecision of results
The limited amount of outcome data available from this single trial did not permit any assessment of the precision of the results.
High probability of publication bias
In view of the low number of trials included in this review this assessment was not estimable.
For further details see summary of findings Table for the main comparison.
Potential biases in the review process
We made strident attempts to limit bias in the review process by ensuring a comprehensive search for potentially eligible studies, which included searching in other than the major databases and which resulted in the retrieval of a number of studies from journals that are not indexed to those major databases. The effects of language bias on the identification and selection of studies is widely recognised and therefore we ensured that all studies that were not in the English language were translated by native language speakers and that this extended to assistance with the assessment of study eligibility and risk of bias. However, we accept that the incompleteness of some of the reports and our inability to obtain clarification of certain trial details or to resolve ambiguities in the reports may have contributed to some bias in their assessment, but where these conditions applied this was explicitly stated in the text of our review.
Agreements and disagreements with other studies or reviews
We are not aware of any other reviews that have considered this research question. DynaMed, which systematically monitors research for clinical practice and is updated daily, did not have additional evidence beyond the evidence summarised in our review (DynaMed 2013).
Study flow diagram.
'Risk of bias' graph: review authors' judgements about each methodological quality item presented as percentages across all included studies.
'Risk of bias' summary: review authors' judgements about each methodological quality item for each included study.
Forest plot of comparison: 1 Pain severity, outcome: 1.1 Day 1.
Forest plot of comparison: 1 Pain severity, outcome: 1.2 Day 3.
Forest plot of comparison: 1 Pain severity, outcome: 1.3 Day 7.
Comparison 1 Lidocaine versus placebo, Outcome 1 Pain: change in severity. Day 1.
Comparison 1 Lidocaine versus placebo, Outcome 2 Pain: change in severity. Day 3.
Comparison 1 Lidocaine versus placebo, Outcome 3 Pain: change in severity. Day 7.
| Core elements | Issues to consider | Status of research for this review |
| Evidence | What is the current state of evidence? | A systematic review identified several RCTs which matched the eligibility criteria, but most of which were inadequately reported and assessed as having 'high' to 'unclear' risk of bias |
| Population | Diagnosis, disease stage, comorbidity, risk factor, sex, age, ethnic group, specific inclusion or exclusion criteria, clinical setting | Patients of any age, gender or ethnic group, without significant comorbidity (e.g. diabetes, chronic lung disease, bleeding disorders), who underwent tonsillectomy, with or without adenoidectomy, by any of the recognised surgical techniques |
| Intervention | Type, frequency, dose, duration, prognostic | Spray, mouthrinse or instilled solution (in different dose, frequency or duration). Compliance to be recorded including any concomitant/rescue medications via pill counts Based on current evidence some of these interventions, in particular lidocaine, have the potential to be effective and this should be further explored in future trials |
| Comparison | Type, frequency, dose, duration, prognostic factor | Placebo with a dose, frequency, duration comparable to the intervention. Compliance to be recorded, including any concomitant/rescue medications via pill counts |
| Outcome | Which clinical or patient‐related outcomes will the researcher need to measure, improve, influence or accomplish? | Pain severity: validated pain scale capable of measuring the multidimensional aspects of pain (sensory dimensions: location, quality, intensity, duration, frequency) VAS: self assessed or carer‐assessed (trained raters) Data: continuous and dichotomous |
| Time stamp | Date of literature search or recommendation | July 2013 |
| Study type | What is the most appropriate study design to address the proposed question? | Randomised controlled trial (adequately powered/large sample size) Methods: concealment of allocation sequence Blinding: patients, therapist, trialists, outcomes assessors, data analysts Setting: inpatient or outpatient care with follow‐up (< 7 days) |
| RCT: randomised controlled trial; VAS: visual analogue scale | ||
| Oral rinses, mouthwashes and sprays to improve recovery after tonsillectomy | ||||||
| Patient or population: patients with tonsillectomy | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | No of participants | Quality of the evidence | Comments | |
| Assumed risk | Corresponding risk | |||||
| Control | Lidocaine | |||||
| Pain: severity score day 1 | The mean pain severity score on day 1 in the control groups was | The mean pain severity score on day 1 in the intervention groups was | 40 | ⊕⊕⊝⊝ | ||
| *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). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1The incompleteness of trial details, and in particular the lack of clarity about sequence generation and concealment, was a serious limitation in the included trial (Kaygusuz 2003). Subjective outcome assessment of pain coupled with potentially inadequate blinding leading to biased assessment of the intervention effect are likely to have further compromised the quality of the evidence. | ||||||
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Pain: change in severity. Day 1 Show forest plot | 1 | 40 | Mean Difference (IV, Random, 95% CI) | ‐2.0 [‐2.79, ‐1.21] |
| 2 Pain: change in severity. Day 3 Show forest plot | 1 | 40 | Mean Difference (IV, Random, 95% CI) | ‐1.2 [‐1.98, ‐0.42] |
| 3 Pain: change in severity. Day 7 Show forest plot | 1 | 40 | Mean Difference (IV, Random, 95% CI) | ‐0.40 [‐0.93, 0.13] |
