Description of the condition
Autism is a complex neurodevelopmental disorder, first described by Leo Kanner in 1943 following observations of 11 children with severe impairments in social communication and social interaction, and repetitive behaviours such as rocking (Kanner 1943). Today, the two main classification systems - the International Classification of Diseases and Related Health Problems, ICD-10 (WHO 1994) and the Diagnostic and Statistical Manual of Mental Disorders, DSM-IV (APA 2000) - outline diagnostic criteria for three core features: impaired social interaction, impaired communication, and stereotypical and repetitive behaviours with detailed descriptions of mild to severe clinical presentations (Waterhouse 1996).
Increasingly, autism spectrum disorder (ASD) is used as an overarching term in clinical and research practice to draw together the conditions of 'classic' autism, Asperger's syndrome and Pervasive Developmental Disorder Not Otherwise Specified (PDD-NOS, or atypical autism). Further support for this practice comes from the 5th revision to the Diagnostic and Statistical Manual of Mental Disorders, in which these separate conditions are grouped together as a single condition of 'autism spectrum disorder'. Clinical presentations vary from the very severely affected individual who is intellectually disabled, unable to communicate, withdrawn and preoccupied with repetitive behaviours, to fairly high-functioning individuals who have odd social and communication mannerisms and narrowly-focused interests (Lord 2012).
Epidemiological studies report an increase in the prevalence of autism. An early study in the United Kindom in 1966 estimated a prevalence of 4.5 cases per 10,000 children (Lotter 1966). In 1992, 19 in every 10,000 six-year-old Americans were diagnosed with autism (Newschaffer 2005). As of 2008, Centers for Disease Control and Prevention (CDC) reported a rate of 11.3 per 1,000 children in the United States (US CDC 2012). The reason for the increase is debated. Increased awareness amongst healthcare professionals and the community, and more help-seeking behaviour are recognised as having an impact on broadened diagnostic criteria. The role of other potential causal and/or contributory factors to the increasing prevalence is less clear.
An early clinical diagnosis of ASD is possible before three years of age (Cox 1999) and as early as eight months (Werner 2000), but the diagnostic stability is low (Woolfenden 2012). Boys are at greater risk than girls for developing autism, as are those who have siblings with autism. It is also more likely to occur in individuals with other developmental disorders such as fragile X syndrome, chromosomal abnormalities, single gene disorders like tuberous sclerosis, gene mutations, and mitochondrial disorders (Smalley 1998; Wassink 2001; Reddy 2005; Schaefer 2008).
The aetiology of this condition is unclear. It is widely accepted that a combination of genetic, and prenatal, perinatal, and postnatal environmental factors disrupt neurodevelopment (Happe 2008; Gardener 2009). The genetic underpinning is strong but it is also complex and as yet not clearly elucidated.
The heterogeneity of the condition and indeterminate aetiology mean treatment is symptomatic. Pharmacological approaches, including the use of new atypical antipsychotics (Ching 2012), and behavioral approaches, such as social skills groups (Reichow 2012a) and Early Intensive Behavioral Intervention (Reichow 2012b), have been described as well as family support, dietary interventions, and educational planning (Srinivasan 2009; Vanderbilt Evidence-Based Practice Center 2011). In the long term, a multidisciplinary approach to assessment, with early identification of deficits and individualised care planning, is thought to provide optimal support for the person with ASD (Myers 2007).
Description of the intervention
Oxytocin is a nonapeptide hormone with multiple sites of action in the human body. It regulates a large number of reproduction-related processes; particularly important is its ability to stimulate uterine contractility (Shmygol 2006). The uterine-contracting property of oxytocin was discovered in 1906 by Dale (Dale 1906). The structure was identified in 1953 by the laboratory of Vincent du Vigneaud (Duvigneaud 1953) and the hormone was soon synthesised in the same laboratory (Duvigneaud 1954). This is the first synthetic, polypeptide hormone produced, and Vincent du Vigneaud was recognised and awarded the Nobel Prize in Chemistry (1955).
In 1979, Pedersen and Prange reported that injection of oxytocin into the brain of female rats brought on full maternal behaviour toward foster pups (Pedersen 1979). This provided a new understanding of the effects of oxytocin in the central nervous system, besides its peripheral effects in female reproduction. Accumulating evidence over past years further supports oxytocin playing an important role in human behaviours and its potential importance in the aetiology and treatment of mental disorders (Ishak 2011; Meyer-Lindenberg 2011).
Intranasal oxytocin (nasal spray) provides a direct pathway to deliver the drug to the central nervous system (Born 2002). Because of both the existence of the blood-brain barrier and the short half-life of oxytocin, the drug is not thought to affect the central nervous system when administered intravenously. Hence, if oxytocin nasal spray is used, behavioural changes after intranasal oxytocin administration could be attributed to the central effects of the drug.
The use of intranasal oxytocin in brain disorders is still at the research stage. Various doses have been used in previous studies. For example, in the first study that investigated the effects of a single dose of intranasal oxytocin on emotion recognition in young people with ASD, 24 IU (4 puffs per nostril, each puff with 3 IU oxytocin) or 18 IU (3 puffs per nostril, each puff with 3 IU oxytocin) were administered (Guastella 2010). Based on a recent systematic review, intranasal oxytocin produces no significant side effects, and is not associated with adverse outcomes when delivered in doses of 18 - 40 IU for short-term use in controlled research settings (MacDonald 2011).
The compound has immediate effects on behaviours but the effects of single-dose administration do not last long. This explains why, in studies that aim to examine the effects of a single-dose administration of oxytocin, behavioural tests must be started quickly following nasal administration. For example, the time between drug administration and the starting of assessment was 50 minutes in the study by Andari 2010, and 45 minutes in the studies by Bartz 2010, Guastella 2010 and Labuschagne 2010. It is not known whether lasting effects can be observed after repeated administration of oxytocin for long-term use, even after stopping the treatment. To make meaningful comparisons and draw valid conclusions, we will conduct subgroup analyses based on the time interval between the last drug administration and outcome measurement, to differentiate long-term effects from acute effects of a single-dose administration.
How the intervention might work
The exact mechanisms by which oxytocin might improve autism symptoms are not clear.
In the human brain, parvocellular neurons in the paraventricular nucleus of the hypothalamus produce and distribute oxytocin directly to the amygdala, hippocampus, striatum, suprachiasmatic nucleus, bed nucleus of stria terminalis and brainstem, where they act as neuromodulators or neurotransmitters, and thereby influence neurotransmission in these areas (Meyer-Lindenberg 2011). Although little information is available about the neural geography of oxytocin receptor distribution in the human brain, it is known that oxytocin affects social affiliative behaviour (Insel 2010) and it is hypothesised that the oxytocin system might be impaired in autism. This is evidenced by the genetic association study of the oxytocin receptor gene (Wu 2005) and the observation that CD38, a protein involved in oxytocin secretion, was significantly reduced in immortalised lymphocytes derived from children with ASD compared to their 'unaffected' parents (Lerer 2010).
The expression of oxytocin receptors in the human brain makes possible the central nervous system effects of administered oxytocin. Theoretically, oxytocin enters the central nervous system directly after nasal administration, binds to oxytocin receptors in various brain regions, and exerts effects on behaviours and symptoms of autism by activating those receptors. The amygdala, functioning as the 'social brain', could be particularly important. Amygdala volume changes have been observed both in people with autism and in their siblings (Rojas 2004; Dalton 2007), and findings from functional magnetic resonance imaging studies support a modulatory role of intranasal oxytocin on amygdala function (Kirsch 2005; Baumgartner 2008; Gamer 2010).
Current literature suggests a therapeutic potential for oxytocin through its effects on core dimensions of ASD (Meyer-Lindenberg 2011). However, it is also argued that oxytocin may not be an 'autism drug', since more general mechanisms, such as anxiolytic effect, may indirectly impact symptoms of the condition (Churchland 2012). It should be acknowledged that human behaviours are extremely complex, as is the symptomatology of autism. A change in behaviour could be due to a direct effect of oxytocin on that behaviour itself, or as a secondary change caused by other direct effects. For example, oxytocin may enhance social interactions by improving decoding of emotional cues and promoting the willingness to take risks in terms of co-operative and trusting behaviours (Meyer-Lindenberg 2011). It is also possible that oxytocin promotes social engagement behaviour by suppressing fear and mistrust (Andari 2010).
Why it is important to do this review
The potential role of oxytocin administered intranasally in improving core symptoms of autism is emerging. It is important to investigate whether the postulated efficacy correlates with genetic variants, behavioural markers or participant characteristics, for example, age, gender, and diagnostic subtype. The safety profile of long-term intranasal oxytocin treatment also remains unknown. Hence, a systematic review is needed of available trial data on the efficacy and safety of intranasal oxytocin in ASD.
Intranasal oxytocin is thought to improve the deficit in social interaction and communication among people with ASD. It may also improve other symptoms such as restricted and repetitive behaviour, and anxiety, as well as global improvement rated by clinicians, and self-reported quality of life.
It is important to differentiate the immediate effects of intranasal oxytocin after single-dose administration from the stable and lasting changes after long-term intervention. We anticipate that some outcome measures (such as the RMET) will show immediate changes after a single-dose administration provided that the test is conducted within a certain period of time (for example, one hour) following drug administration. Those changes will disappear without further administration of the drug, but it is possible that the changes will be stabilised after a period of continued treatment. We expect that some outcome measures (such as the Vineland) will not show detectable change after a short-term intervention. However, after long-term intervention (for example, more than 12 weeks), there could be stable and long-lasting change despite discontinuing drug treatment.
To assess the efficacy of intranasal oxytocin in improving social interaction and communication deficit, and other clinical outcomes in autism spectrum disorders (ASD), and to examine its safety.
Criteria for considering studies for this review
Types of studies
Randomised and blinded controlled trials.
Types of participants
Children and adults with a clinical diagnosis of an autism spectrum disorder (ASD) made by a clinician based on diagnostic criteria in the Diagnostic and Statistical Mannual of Mental Disorders (DSM-IV) (APA 2000) or the International Statistical Classification of Diseases and Related Health Problems (ICD-10) systems (WHO 1994). In the DSM-IV system, ASD includes Autistic Disorder, Asperger's Disorder, and Pervasive Developmental Disorder Not Otherwise Specified; in the ICD-10 system, it includes Childhood Autism, Atypical Autism, Asperger's Syndrome, Other Pervasive Developmental Disorder, and Pervasive Developmental Disorder Unspecified.
We will include participants who fulfil diagnostic criteria before and after DSM-IV and ICD-10: Infantile Autism (IA full syndrome and IA residual state), Childhood Onset Pervasive Developmental Disorder (COPDD full syndrome and COPDD residual state), and Atypical Pervasive Developmental Disorder in DSM-III; Autistic Disorder and Pervasive Developmental Disorder Not Otherwise Specified in DSM-III-R; Infantile Autism in ICD-9; Autism Spectrum Disorders in DSM-5.0.
Types of interventions
Intranasal oxytocin administered at any dosage and for any duration against a placebo. We will include trials that give oxytocin against placebo and also offer adjunctive treatments that are provided to participants in each (all) arms.
The optimal dosage of nasal administration of oxytocin for the treatment of ASD is unknown. In both of the first two published trials, the researchers chose a dosage of 24 IU and reported that at this dosage, oxytocin nasal spray produced statistically significant behaviour change as measured by the Reading the Mind in the Eyes Task (RMET) (Guastella 2010) or a social ball-tossing game (Andari 2010). Since 24 IU is a common dosage that has been used in intranasal oxytocin research and, given the fact that observable changes has been reported at this dosage, we plan to use 24 IU as the cut-off value for dosage in subgroup analysis.
Types of outcome measures
- Social interaction, measured by corresponding score from validated tools such as the Vineland Adaptive Behaviour Scales, Second Edition (Vineland-II) (Sparrow 2005) and the Adaptive Behaviour Assessment System, Second Edition (ABAS-II) (Harrison 2008) or standard social cognition test such as the Reading the Mind in the Eyes Test (RMET).
- Communication: measured by corresponding score from validated tools such as the Vineland-II and the ABAS-II.
- Adverse effects: central nervous system disorders such as headache, light headedness or vertigo or both, drowsiness or sleepiness or both; cardiac system disorders such as tachycardia, bradycardia, and arrhythmia; gastrointestinal system disorders such as nausea and vomiting; skin and subcutaneous tissue disorders such as rash.
- Stereotyped behaviours and restricted interests: measured by scales such as the Repetitive Behaviour Scale - Revised (RBS-R) (Bodfish 2000).
- Anxiety: measured by scales such as the State–Trait Anxiety Inventory for Children (STAIC) (Spielberger 1973).
- Quality of life: measured by scales such as the 12-item Short Form Health Survey (SF-12) (Ware 1996).
- Parent stress: measured by scales such as the Parenting Stress Index (PSI) (Abidin 1997).
We will synthesise results for the following time points: within 24 hours of the first dosage, more than one day but less than one week, one to five weeks, six to 12 weeks, and over 12 weeks.
We will include all three primary outcomes and secondary outcomes 1, 2 and 4 in a 'Summary of findings' table.
Search methods for identification of studies
We will search the following databases and trials registers. There will be no date or language restrictions.
- Cochrane Central Register of Controlled Trials (CENTRAL)
- Ovid MEDLINE
- Science Citation Index (SCI)
- Social Science Citation Index (SSCI)
- Conference Proceedings Citation Index – Science
- Conference Proceedings Citation Index – Social Sciences & Humanities
- Cochrane Database of Systematic Reviews (CDSR)
- Database of Abstracts of Reviews of Effects (DARE)
- OCLC WorldCat www.worldcat.org/
- ClinicalTrials.gov clinicaltrials.gov/
- International Clinical Trials Registry Platform (ICTRP) apps.who.int/trialsearch/
- metaRegister of Controlled Trials (mRCT) controlled-trials.com/mrct/
We will use the following search strategy for Ovid MEDLINE, and modify it for other databases.
1 exp child development disorders, pervasive/
2 Developmental Disabilities/
3 pervasive development$ disorder$.tw.
4 (pervasive adj3 child$).tw.
5 (PDD or PDDs or PDD-NOS or ASD or ASDs).tw.
9 childhood schizophrenia.tw.
18 11 and 17
Searching other resources
We will handsearch the reference lists of relevant articles and reviews for studies not already identified by the electronic searches. We will contact manufacturers of intranasal oxytocin to determine whether there are any ongoing clinical trials or unpublished results. We also will contact experts in the field to ask if they know of any other unpublished data or ongoing studies.
Data collection and analysis
Selection of studies
Two review authors (LF and JCMW) will independently examine all titles and abstracts obtained from the searches to select potentially relevant studies. The same review authors will obtain full-text articles and read them in detail independently in order to determine the eligibility of each study. The review authors will not be blinded to the names of the authors, institutions, journal of publication or results when they apply the eligibility criteria. In the event of disagreement on whether a study should be included, we will resolve this by face-to-face discussion, and by referral to a third review author (RM or MDS) if we cannot reach a consensus. LF will create a unique study ID and report ID for each study or report included in the review.
We will retrieve any paper where it is not clear from the title and abstract whether or not it is eligible.
Data extraction and management
Two review authors (LF and JCMW) will extract the data from all included trials and enter them into a predesigned data extraction form independently. Data to be extracted are listed in Appendix 1. We will compare both sets of extracted data to ensure accuracy, and will resolve discrepancies by discussion. One review author (LF) will enter data into Review Manager 5 software (RevMan 2012) and a second author (JCMW) will check them.
Assessment of risk of bias in included studies
Two review authors (LF and JCMW) will independently assess the risk of bias of each included study according to the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a).
We will assess the risk of bias of each included study using the Cochrane 'Risk of bias' tool for the following domains, with ratings of low, high or unclear risk of bias. We will base the judgements on the detailed considerations that are provided in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). We will provide information that supports each judgement in the 'Risk of bias' tables, and we will also provide a source of information for each of the 'Risk of bias' assessments. We will state clearly where judgements are based on information provided outside publicly available documents. If there is any disagreement about the risk of bias of any included study, we will consult the third review author (RM) to resolve the disagreement.
Random sequence generation
1. Low risk of bias: if there was a random component in the sequence generation process, for example, referring to a random number table or using a computer random number generator.
2. High risk of bias: if there was a non-random component in the sequence generation process, for example, sequence generated by odd or even date of birth.
3. Unclear risk of bias: if there was insufficient information about the sequence generation process to permit a judgement of low or high risk of bias.
1. Low risk of bias: if the allocation of participants involved central allocation, sequentially-numbered drug containers of identical appearance or sequentially numbered, opaque, sealed envelopes.
2. High risk of bias: if the allocation sequence was known to the investigators or participants.
3. Unclear risk of bias: if the trial was described as randomised, but the method used to conceal the allocation was not described.
Blinding of participants and personnel
1. Low risk of bias: if blinding of participants and key study personnel was ensured and it was unlikely that it could have been broken, or if the outcome was not likely to be influenced by a lack of blinding.
2. High risk of bias: if blinding of participants and key study personnel was not done or was broken, and if the outcome was likely to be influenced by lack of blinding.
3. Unclear risk of bias: if the term 'blinding' was mentioned, but no details were given for who was blinded and how the blinding was ensured to permit a judgement of low or high risk.
Blinding of outcome assessment
1. Low risk of bias: if the outcome assessors were blinded to the intervention received by the participants, or if the outcome was not likely to be influenced by lack of blinding.
2. High risk of bias: if no blinding of outcome assessment was mentioned but measurement was likely to be influenced by lack of blinding, or where blinding could have been broken.
3. Unclear risk of bias: if the term 'double-blinded' was mentioned, but no details were given with regards to how the outcome assessors were blinded to the intervention received by the participants.
Incomplete outcome data
1. Low risk of bias: if there were no missing outcome data, or the reasons for missing data were unlikely to be related to the true study outcome, or the numbers and reasons were balanced across intervention groups.
2. High risk of bias: if there were missing outcome data and the reasons are likely to be related to true study outcome with either imbalance in numbers or reasons for missing data across intervention groups.
3. Unclear risk of bias: if there was insufficient reporting of attrition and/or exclusion to permit a judgement of low or high risk risk of bias.
For studies at high and unclear risk of bias, we will seek to obtain missing data and the reasons for missing data from the study authors, and will seek to conduct statistical analysis with re-inclusions of data that are obtained from study authors. We will then re-rate the risk of bias.
We will assess the possibility of selective outcome reporting by checking study protocols, if available, and comparing the outcomes listed in the protocol with the published study report.
1. Low risk of bias: if it is clear that all of the study’s prespecified and expected outcomes that are of interest in the review have been reported in the prespecified way.
2. High risk of bias: if not all the study’s prespecified outcomes have been reported, or if one or more primary outcomes were reported in a way that was not prespecified, or if one or more reported primary outcomes were not prespecified, or if one or more outcomes of interest in the review were reported incompletely so that they cannot be entered in a meta-analysis, or if the study failed to include results of a key outcome that would be expected to have been reported.
3. Unclear risk of bias: if there is insufficient information to permit a judgement of low or high risk of bias.
Other sources of bias
1. Low risk of bias: if the study appears to be free of other sources of bias.
2. High risk of bias: if there was at least one problem in the study that could put it at risk of bias. For example, if the study has been claimed to have been fraudulent, or if there was extreme baseline imbalance.
3. Unclear risk of bias: if there is a lack of information to permit a judgement of low or high risk of bias.
For overall risk of bias, we will consider studies that have adequate random sequence generation, adequate allocation concealment, adequate blinding, adequate handling of incomplete outcome data, no selective outcome reporting, and are without other bias risks, as being at overall low risk of bias. We will consider studies that are assessed as at being at high or unclear risk of bias in the majority of domains as being at overall high risk of bias. We will consider the remaining studies to be at moderate risk of bias.
Measures of treatment effect
We will use risk ratio (RR) estimates with 95% confidence intervals (CI) for dichotomous variables. We have decided not to use the odds ratio (OR) because it could overestimate the treatment effect for common study outcomes. However, the RR is not mathematically ‘invertible’. For adverse events, the RR of having an adverse event is not the direct reciprocal of the RR of not having an adverse event. The review authors will clearly state this when they analyse, interpret, and discuss the results for adverse events.
If a potential study does not report information on the 2 x 2 table or the RR, the review authors will contact the corresponding author of the study to obtain the information. The review authors will seek to compute the RR using the formulae given in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2011) when information on effect size is available in other forms.
We will calculate mean differences when studies use the same measurement, and standardised mean differences when studies use different scales.
If a study has not reported standard deviations or standard errors, the review authors will contact the corresponding author of the study to obtain the information. If necessary, the review authors will seek to calculate effect estimates from P values, t statistics, ANOVA tables or other statistics as appropriate.
If a study analyses skewed data with parametric methods without transforming the raw data prior to analysis, the review authors will contact the corresponding author of the study to obtain the raw data, will perform appropriate transformation (for example, logarithmic transformation), and will then include the results based on the transformed data in the meta-analysis. If the raw data from a particular study are not available after every effort has been made to source them, we will exclude the study from analysis.
If a study only reports change from baseline data, the review authors will contact the corresponding author of the study to obtain data at each available time point. If such information from a particular study is not available after every effort has been made to source it, we will exclude the study from analysis.
A study may use multiple, interchangeable measures of the same construct at the same point in time. For dichotomous measures, we will choose only one outcome measure for analysis based on the trial authors' statement in their report as well as our own judgement (LF and JCMW) as regards the superiority of the measures. For continuous measures, we will pool all interchangeable measures together using the mean value of the standardised mean difference (SMD) of all measures.
Unit of analysis issues
When conducting a meta-analysis combining the results of cross-over trials, we will use the inverse variance methods recommended by Elbourne 2002. In the case that data from a cross-over trial are limited and restricted, we will use the presented data within the first phase only, up to the point of cross-over. If repeated observations of participants are reported, we will define several different outcomes, based on different periods of follow-up, and will perform separate analyses.
We will analyse trials that include oxytocin against placebo and also offer adjunctive treatments that are provided to participants in all arms without considering the adjunctive treatments. The effects of the adjunctive treatments are not part of the research question, and we expect the distributions to be equal across all arms.
For multi-arm studies that include treatment arms with intranasal oxytocin at different dosage (for example, 24 IU/day in one arm, 48 IU/day in another arm) in addition to a placebo group, we will include all participants in the overall meta-analysis, and include participants in the corresponding subgroup based on the dosage they received in the subgroup analysis. We will determine the number of controls in the overall analysis and each of the subgroup analyses by the number of participants in the common placebo control arm.
For multi-arm studies that include treatment arms with intranasal oxytocin alone, and a combination of oxytocin with another treatment (for example, oxytocin 24 IU/day in one arm, oxytocin 24 IU/day and social skill training in another arm) in addition to a placebo group, we will only include the oxytocin-alone group in the meta-analysis.
Dealing with missing data
Review authors will attempt to obtain data missing from included trials by contacting study authors. We will describe missing data and drop-out or attrition or both for each trial included in the review in the 'Risk of bias' table, and will assess and discuss the extent to which missing data could alter the results and conclusion. We will also describe and assess the difference in the proportion and reasons for missing data across intervention groups.
We will use sensitivity analysis to detect any differences between the per-protocol analysis and the intention-to-treat analysis data. For dichotomous outcomes, we will base sensitivity analysis on consideration of ‘best-case’ and ‘worst-case’ scenarios.
Assessment of heterogeneity
We will assess clinical heterogeneity by comparing the variability between trials with respect to participant factors (age, gender, diagnostic subtypes) and intervention factors (dose, duration). We will assess methodological heterogeneity by comparing the differences between the trials' methodological factors such as concealment of allocation, blinding, and the ways in which the outcomes are defined and measured. We will assess the presence of statistical heterogeneity by visual inspection of the forest plot and formal Chi² test. The Chi² test assesses whether observed differences in results are compatible with chance alone. A low P value provides evidence of heterogeneity of intervention effects (variation in effect estimates beyond chance). We will use the I² statistic to quantify inconsistency across studies. This statistic describes the percentage of the variability in effect estimates that is due to heterogeneity rather than to sampling error (chance). The presence of heterogeneity will be defined by a P value of less than 0.05 from the Chi² test and an I² value of 75% to 100%. Given limitations of the methods, the P value from the Chi² test and the value of I² will be taken only as a guide, and the review authors will exercise caution when interpreting the results.
In the case of substantial heterogeneity, the review authors will explore the reasons by conducting subgroup analysis based on age, gender, diagnostic subtype, oxytocin dosage, and intervention duration.
If it is evident from the subgroup analyses that any of the above factors affect the effect size of the intervention, we will report the results, compare them with the results from the primary analysis, and provide adequate discussions of the influences of such factors on the main results of the primary analysis with all participants.
Assessment of reporting biases
We will use the funnel plot (intervention effect estimate versus standard error of intervention effect estimate) to assess publication bias if there are sufficient studies (10 or more for an outcome). If we find funnel plot asymmetry, we will further investigate clinical diversity of studies as a possible explanation. If there are enough studies, we also will use the 'contour-enhanced' funnel plot proposed by Peters 2008 to differentiate asymmetry due to publication bias from that due to other factors. If the supposed missing studies are in areas of higher statistical significance, this would suggest the cause of the asymmetry is more likely to be due to factors other than publication bias.
If there is no important clinical and methodological heterogeneity (age, gender, diagnostic subtype, oxytocin dosage, intervention duration), we will perform meta-analysis with synthesised data from all included studies. We will use both the fixed-effect model and the random-effects model, because the two methods are based on different assumptions, and we are not sure which assumption will be more appropriate. The fixed-effect model assumes that the true effect of intervention is the same in every study and the observed differences are solely due to chance. In contrast, the random-effects model assumes that true between-study heterogeneity exists and this heterogeneity is taken into account in the calculations. In the absence of heterogeneity, fixed-effect and random-effects models should yield the same results, and we will report the results from the fixed-effect model only. If there is significant heterogeneity, the results will be different and we will report the results from the random-effects model only.
If meta-analysis is unsuitable, we will describe the results of each trial individually with respect to the primary and secondary outcomes listed above.
Subgroup analysis and investigation of heterogeneity
If there is a sufficient number (at least 3 for each subgroup) of studies, we will perform the following exploratory subgroup analyses.
- Age: adults versus children
- Diagnostic subtypes: Autistic disorder versus Asperger's syndrome
- Drug dosage: ≤ 24 IU versus > 24 IU
- Duration: one dose only on a single day; 2 days to 12 weeks; > 12 weeks
- Time interval between the last dosage and the commencement of outcome measurement: within 1 hour versus > 1 hour
We will conduct sensitivity analysis to assess the impact of studies with different levels of risk of bias. For example, we will exclude from the meta-analysis studies at high risk of bias for sequence generation or allocation concealment or both, to determine whether the results and conclusions remain unchanged. We will also conduct sensitivity analysis to compare the results with the choice of fixed-effect or random-effects models.
We thank Margaret Anderson (Trials Search Co-ordinator for CDPLP) for helping us to develop the search strategy .
Appendix 1. Study data to be extracted
- Study design (for example, parallel or cross-over design)
- Total study duration
- Method of randomisation
- Methods of allocation concealment
- Inclusion and exclusion criteria
- Total number of participants
- Diagnostic criteria
- Diagnostic subtypes and number of participants for each subtype
- Loss to follow-up
- Total number of intervention groups
- Intervention details for each intervention and comparison group (for example, dosage, frequency, duration)
- Outcome and time points (i) collected; (ii) reported
For each outcome of interest
- Outcome definition
- Unit of measurement
- For scales: upper and lower limits, and whether high or low score is good
- Methods of analysis (intention-to-treat or per-protocol analysis)
- Statistical techniques
- Comparability of groups at baseline
- Number of participants allocated to each intervention group.
For each outcome of interest
- Sample size
- Missing participants
- Summary data for each intervention group (2 x 2 table for dichotomous data; means and SDs for continuous data)
- Estimate of effect with confidence interval; P value
- Dates study was conducted
- Details of funding sources
- Possible conflicts of interest
Contributions of authors
John CM Wong and Lei Feng proposed this systematic review. Lei Feng, John CM Wong, and Rathi Mahendran wrote the study protocol. Michael Spencer and Edwin Chan reviewed and revised the study protocol.
Declarations of interest
Lei Feng - none known.
John CM Wong - none known.
Rathi Mahendran - none known.
Edwin SY Chan - none known.
Michael D Spencer - No payments, fees or any other potential financial conflicts of interest arise in respect of this work. He is employed by the University of Cambridge as a Senior Clinical Research Associate. He holds an MRC Clinician Scientist Fellowship, awarded in the field of autism neuroimaging research. In the course of his work, he attends conferences relating to autism research, with travel, accommodation, and meeting expenses paid by the University of Cambridge.