human
***TASK*** the task is to summarize an input biomedical literature in six sentences 
    ***INPUT*** the input is a biomedical literature 
    ***OUTPUT*** the output is the summary of an input biomedical literature in six sentences 
    ***DOCUMENTATION*** 
    ***EXAMPLES*** 
    Input: One hundred and fifty children aged between 2 and 9 years with bilateral SOM were allocated at r and om to three groups : Adeno-tonsillectomy ( 47 cases ) , adenoidectomy ( 47 cases ) and neither procedure ( 53 cases ) . A further 42 children were allocated to either adenoidectomy or no surgery . In all only one ear was treated at r and om by myringotomy and insertion of a ventilation tube . The unoperated ear was examined six weeks , six months , nine months , one , two and three years post-operatively for otoscopic clearance of the effusion , impedance change and improvement in mean hearing threshold . Thus the effects on middle ear status of adenoidectomy alone and in combination with tonsillectomy were assessed . There was a significant clearance of middle ear fluid , change from no peak to peak impedance measurement and hearing gain as a result of both procedures with a late trend favouring the combined operation . Neither pre-operative tonsils size nor the number of attacks of tonsillitis affect outcome . However there is a relationship between age and radiographic post-nasal space airway size with clearance of the effusion one year after surgery . These findings permit recommendation for adenoidectomy with improved expectation for resolution of SOM if cases are selected with reference to these two variables . They also suggest in which cases the operation should not be recommended . Despite the trends in outcome favouring combined operations , the extra morbidity associated with the addition of tonsillectomy does not at present justify recommendation for removal of the tonsils in addition to adenoidectomy for cases with SOM . Tonsillectomy in these children should be assessed on grounds of tonsillar pathology per se and not on the status of the middle ear Abstract  Variability  in patients ' response to interventions in pain and other clinical setting s is large . Many explanations such as trial methods , environment or culture have been proposed , but this paper sets out to show that the main cause of the variability may be r and om chance , and that if trials are small their estimate of magnitude of effect may be incorrect , simply because of the r and om play of chance . This is highly relevant to the questions of ‘ How large do trials have to be for statistical accuracy ? ’ and ‘ How large do trials have to be for their results to be clinical ly valid ? ’ The true underlying control event rate ( CER ) and experimental event rate ( EER ) were determined from single‐dose acute pain analgesic trials in over 5000 patients . Trial group size required to obtain statistically significant and clinical ly relevant ( 0.95 probability of number‐needed‐to‐treat within ±0.5 of its true value ) results were computed using these values . Ten thous and trials using these CER and EER values were simulated using varying group sizes to investigate the variation due to r and om chance alone . Most common analgesics have EERs in the range 0.4–0.6 and CER of about 0.19 . With such efficacy , to have a 90 % chance of obtaining a statistically significant result in the correct direction requires group sizes in the range 30–60 . For clinical relevance nearly 500 patients are required in each group . Only with an extremely effective drug ( EER>0.8 ) will we be reasonably sure of obtaining a clinical ly relevant NNT with commonly used group sizes of around 40 patients per treatment arm . The simulated trials showed substantial variation in CER and EER , with the probability of obtaining the correct values improving as group size increased . We contend that much of the variability in control and experimental event rates is due to r and om chance alone . Single small trials are unlikely to be correct . If we want to be sure of getting correct ( clinical ly relevant ) results in clinical trials we must study more patients . Credible estimates of clinical efficacy are only likely to come from large trials or from pooling multiple trials of conventional ( small ) size BACKGROUND Traditional and largely qualitative review s of evidence are now giving way to much more structured systematic overviews that use a quantitative method to calculate the overall effect of treatment . The latter approach is dependent on the quality of primary studies , which may introduce bias if they are of poor method ologic quality . OBJECTIVE To test the hypothesis that the inclusion of poor- quality trials in meta-analyses would bias the conclusions and produce incorrect estimates of treatment effect . METHODS An overview of r and omized trials of antiestrogen therapy in subfertile men with oligospermia was performed to test the hypothesis . Data sources included online search ing of MEDLINE and Science Citation Index data bases between 1966 and 1994 , scanning the bibliography of known primary studies and review articles , and contacting experts in the field . After independent , blind assessment , nine of 149 originally identified studies met the inclusion criteria and were selected . We assessed study quality independently . Outcome data from each study were pooled and statistically summarized . RESULTS There was a marginal improvement in pregnancy rate with antiestrogen treatment ( odds ratio , 1.6 ; 95 % confidence interval , 0.9 to 2.6 ) . Sensitivity analyses on the basis of method ologic quality demonstrated that poor- quality studies produced a positive effect with treatment , whereas no benefit was observed with high- quality studies . CONCLUSION The results of a meta- analysis are influenced by the quality of the primary studies included . Method ologically , poor studies tend to exaggerate the overall estimate of treatment effect and may lead to incorrect inferences One hundred and ninety-one children who presented to the author 's clinic with otitis media with effusion ( OME ) over a 2-year period ( 1986 - 1988 ) have been studied prospect ively . Resolution of their OME was considered to have occurred when they had normal findings on  pneumatic otoscopy , tympanometry and audiometry on at least two occasions 6 months apart and had subjectively normal hearing in between . The number of operations performed during the course of the disease was used as a surrogate for chronicity .  Children with a history of previous aural discharge at presentation were significantly more likely to have chronic OME ( P = < 0.02 ) As professionals , we want to use the best treatments ; as patients , we want to be given them . Knowing whether an intervention works ( or does not work ) is fundamental to clinical decision making . However , clinical decision making involves more than simply taking published results of research directly to the bedside . Physicians need to consider how similar their patients are to those in the published studies , to take the values and preferences of their patients into account , and to consider their own experience with a given test or treatment . Evidence from clinical research is becoming increasingly important in medical- practice decisions as more and better evidence is published . But when is the evidence strong enough to justify changing a practice ? Individual studies that involve only small numbers of patients may have results that are distorted by the r and om play of chance and thus lead to less than optimal decisions . As is clear from other papers in this series , systematic review s identify , critically appraise , and review all the relevant studies on a clinical question and are more likely to give a valid answer . They use explicit methods and quality st and ards to reduce bias . Their results are the closest we can come to reaching the truth given our current state of knowledge . The questions about an intervention that a systematic review should answer are the following : 1 . Does it work ? 2 . If it works , how well does it work in general and compared with placebo , no treatment , or other interventions that are currently in use ? 3 . Is it safe ? 4 . Will it be safe and effective for my patients ? Whereas the critical appraisal and qualitative synthesis provided by review articles can be interpreted directly , the numerical products of quantitative review s can be more difficult to underst and and apply in daily clinical practice . This paper provides guidance on how to interpret the numerical and statistical results of systematic review s , translate these results into more underst and able terms , and apply them directly to individual patients . Many of these principles can also be used to interpret the numerical results of individual clinical studies . They are particularly relevant to systematic review s , however , because such review s contain more information than do primary studies and often exert greater influence than do individual studies . Making Sense of the Numerical Results of Clinical Studies Although the results of clinical studies can be expressed in intuitively meaningful ways , such results do not always easily translate into clinical decision making . For example , results are frequently expressed in terms of risk , which is an expression of the frequency of a given outcome . ( Risks are probabilities , which can vary between 0.0 and 1.0 . A probability of 0.0 means that the event will never happen , and a probability of 1.0 means that it always happens . ) Consider a hypothetical study of the recurrence of migraine headaches in a control group receiving placebo and a treatment group receiving a new antimigraine preparation , drug M ( a secondary prevention trial ) . Suppose that at the end of the trial , migraines recurred in 30 % of the control group ( the risk for recurrence was 0.30 ) but in only 5 % of the drug M group ( risk of 0.05 ) ( Table 1 ) . Table 1 . Numerical Expression of Hypothetical Clinical Trial Results The outcomes of the study are clear enough for the two groups when they are examined separately . But clinicians and patients are more interested in the comparative results , that is , the outcome in one group relative to the outcome in the other group . This overall ( comparative ) result can be expressed in various ways . For example , the relative risk , which is the risk in the treatment group relative to that in the control group , is simply the ratio of the risks in the two groups . In other words , relative risk is the risk in the treatment group divided by that in the control group , 0.05 0.30 , or 0.17 . The comparison can also be expressed as the reduction in relative risk , which is the ratio between the decrease in risk ( in the treatment group ) and the risk in the control group , 0.25 0.30 , or 0.83 ( Table 1 ) . ( The relative risk reduction can also be calculated as 1 relative risk ) . Although the clinical meaning of relative risk ( and relative risk reduction ) is reasonably clear , relative risk has the distinct disadvantage that a given value ( for example , 0.17 ) is the same whether the risk with treatment decreases from 0.80 to 0.14 , from 0.30 to 0.05 , from 0.001 to 0.00017 , and so forth . The clinical implication s of these changes clearly differ from one another enormously and depend on the specific disease and intervention . An important alternate expression of comparative results , therefore , is the absolute risk reduction . Absolute risk reduction is determined by subtracting the risk in one group from the risk in the other ( for example , the risk in the treatment group is subtracted from the risk in the placebo group ) . In the case of our migraine study , the absolute risk reduction would be 0.30 0.05 , which equals 0.25 , or 25 percentage points . In contrast , for a study in which the risk decreased from 0.001 to 0.00017 , the absolute risk reduction would be only 0.00083 , or 0.083 percentage points , which is a trivial change in comparison ( Table 1 ) . This arithmetic emphasizes the difficulty of expressing the results of clinical studies in meaningful ways . Relative risk and relative risk reduction clearly give a quantitative sense of the effects of an intervention in proportional terms but provide no clue about the size of an effect on an absolute scale . In contrast , although it tells less about proportional effects , absolute risk says a great deal about whether an effect is likely to be clinical ly meaningful . Despite this benefit , even absolute risk is problematic because it is a dimensionless , abstract number ; that is , it lacks a direct connection with the clinical situation in which the patient and physician exist . However , another way of expressing clinical research results can provide that clinical link : the number needed to treat ( NNT ) . Number Needed To Treat The NNT for a given therapy is simply the reciprocal of the absolute risk reduction for that treatment [ 1 , 2 ] . In the case of our hypothetical migraine study ( in which risk decreased from 0.30 without treatment with drug M to 0.05 with treatment with drug M , for a relative risk of 0.17 , a relative risk reduction of 0.83 , and an absolute risk reduction of 0.25 ) , the NNT would be 1 0.25 , or 4 . In concrete clinical terms , an NNT of 4 means that you would need to treat four patients with drug M to prevent migraine from recurring in one patient . To emphasize the difference between the concepts embodied in NNT and relative risk , recall the various situations mentioned above , in all of which the relative risk was 0.17 but in which the absolute risk decreased from 0.80 to 0.14 in one case and from 0.001 to 0.00017 in another . Note that the corresponding NNTs in these two other cases are 1.5 and 1204 , respectively : that is , you would need to treat 1.5 and 1204 patients to obtain a therapeutic result in these two situations compared with 4 patients with drug M ( Table 1 ) . The NNT can be calculated easily and kept as a single numerical reminder of the effectiveness ( or , as we will see , the potential for harm ) of a particular therapy . As we suggested , the NNT has the crucial advantage of direct applicability to clinical practice because it shows the effort that is required to achieve a particular therapeutic target . The NNT has the additional advantage that it can be applied to any beneficial outcome or any adverse event ( when it becomes the number needed to harm [ NNH ] ) . The concept of NNT always refers to a comparison group ( in which patients receive placebo , no treatment , or some other treatment ) , a particular treatment outcome , and a defined period of treatment . In other words , the NNT is the number of patients that you will need to treat with drug or treatment A to achieve an improvement in outcome compared with drug or treatment B for a treatment period of C weeks ( or other unit of time ) . To be fully specified , NNT and NNH must always specify the comparator , the therapeutic outcome , and the duration of treatment that is necessary to achieve the outcome . Important Qualities of the Number Needed To Treat The NNT is treatment specific . It describes the difference between treatment and control in achieving a particular clinical outcome . Table 2 shows NNTs from a selection of systematic review s and large r and omized , controlled trials . Table 2 . Numbers Needed To Treat from Systematic Review s and R and omized , Controlled Trials A very small NNT ( that is , one that approaches 1 ) means that a 
    Output:
    
agent
ConclusionS -carboxymethylcysteine is effective in the treatment of children with glue ear .
***TASK*** the task is to summarize an input biomedical literature in six sentences 
    ***INPUT*** the input is a biomedical literature 
    ***OUTPUT*** the output is the summary of an input biomedical literature in six sentences 
    ***DOCUMENTATION*** 
    ***EXAMPLES*** 
    Input: One hundred and fifty children aged between 2 and 9 years with bilateral SOM were allocated at r and om to three groups : Adeno-tonsillectomy ( 47 cases ) , adenoidectomy ( 47 cases ) and neither procedure ( 53 cases ) . A further 42 children were allocated to either adenoidectomy or no surgery . In all only one ear was treated at r and om by myringotomy and insertion of a ventilation tube . The unoperated ear was examined six weeks , six months , nine months , one , two and three years post-operatively for otoscopic clearance of the effusion , impedance change and improvement in mean hearing threshold . Thus the effects on middle ear status of adenoidectomy alone and in combination with tonsillectomy were assessed . There was a significant clearance of middle ear fluid , change from no peak to peak impedance measurement and hearing gain as a result of both procedures with a late trend favouring the combined operation . Neither pre-operative tonsils size nor the number of attacks of tonsillitis affect outcome . However there is a relationship between age and radiographic post-nasal space airway size with clearance of the effusion one year after surgery . These findings permit recommendation for adenoidectomy with improved expectation for resolution of SOM if cases are selected with reference to these two variables . They also suggest in which cases the operation should not be recommended . Despite the trends in outcome favouring combined operations , the extra morbidity associated with the addition of tonsillectomy does not at present justify recommendation for removal of the tonsils in addition to adenoidectomy for cases with SOM . Tonsillectomy in these children should be assessed on grounds of tonsillar pathology per se and not on the status of the middle ear Abstract  Variability  in patients ' response to interventions in pain and other clinical setting s is large . Many explanations such as trial methods , environment or culture have been proposed , but this paper sets out to show that the main cause of the variability may be r and om chance , and that if trials are small their estimate of magnitude of effect may be incorrect , simply because of the r and om play of chance . This is highly relevant to the questions of ‘ How large do trials have to be for statistical accuracy ? ’ and ‘ How large do trials have to be for their results to be clinical ly valid ? ’ The true underlying control event rate ( CER ) and experimental event rate ( EER ) were determined from single‐dose acute pain analgesic trials in over 5000 patients . Trial group size required to obtain statistically significant and clinical ly relevant ( 0.95 probability of number‐needed‐to‐treat within ±0.5 of its true value ) results were computed using these values . Ten thous and trials using these CER and EER values were simulated using varying group sizes to investigate the variation due to r and om chance alone . Most common analgesics have EERs in the range 0.4–0.6 and CER of about 0.19 . With such efficacy , to have a 90 % chance of obtaining a statistically significant result in the correct direction requires group sizes in the range 30–60 . For clinical relevance nearly 500 patients are required in each group . Only with an extremely effective drug ( EER>0.8 ) will we be reasonably sure of obtaining a clinical ly relevant NNT with commonly used group sizes of around 40 patients per treatment arm . The simulated trials showed substantial variation in CER and EER , with the probability of obtaining the correct values improving as group size increased . We contend that much of the variability in control and experimental event rates is due to r and om chance alone . Single small trials are unlikely to be correct . If we want to be sure of getting correct ( clinical ly relevant ) results in clinical trials we must study more patients . Credible estimates of clinical efficacy are only likely to come from large trials or from pooling multiple trials of conventional ( small ) size BACKGROUND Traditional and largely qualitative review s of evidence are now giving way to much more structured systematic overviews that use a quantitative method to calculate the overall effect of treatment . The latter approach is dependent on the quality of primary studies , which may introduce bias if they are of poor method ologic quality . OBJECTIVE To test the hypothesis that the inclusion of poor- quality trials in meta-analyses would bias the conclusions and produce incorrect estimates of treatment effect . METHODS An overview of r and omized trials of antiestrogen therapy in subfertile men with oligospermia was performed to test the hypothesis . Data sources included online search ing of MEDLINE and Science Citation Index data bases between 1966 and 1994 , scanning the bibliography of known primary studies and review articles , and contacting experts in the field . After independent , blind assessment , nine of 149 originally identified studies met the inclusion criteria and were selected . We assessed study quality independently . Outcome data from each study were pooled and statistically summarized . RESULTS There was a marginal improvement in pregnancy rate with antiestrogen treatment ( odds ratio , 1.6 ; 95 % confidence interval , 0.9 to 2.6 ) . Sensitivity analyses on the basis of method ologic quality demonstrated that poor- quality studies produced a positive effect with treatment , whereas no benefit was observed with high- quality studies . CONCLUSION The results of a meta- analysis are influenced by the quality of the primary studies included . Method ologically , poor studies tend to exaggerate the overall estimate of treatment effect and may lead to incorrect inferences One hundred and ninety-one children who presented to the author 's clinic with otitis media with effusion ( OME ) over a 2-year period ( 1986 - 1988 ) have been studied prospect ively . Resolution of their OME was considered to have occurred when they had normal findings on  pneumatic otoscopy , tympanometry and audiometry on at least two occasions 6 months apart and had subjectively normal hearing in between . The number of operations performed during the course of the disease was used as a surrogate for chronicity .  Children with a history of previous aural discharge at presentation were significantly more likely to have chronic OME ( P = < 0.02 ) As professionals , we want to use the best treatments ; as patients , we want to be given them . Knowing whether an intervention works ( or does not work ) is fundamental to clinical decision making . However , clinical decision making involves more than simply taking published results of research directly to the bedside . Physicians need to consider how similar their patients are to those in the published studies , to take the values and preferences of their patients into account , and to consider their own experience with a given test or treatment . Evidence from clinical research is becoming increasingly important in medical- practice decisions as more and better evidence is published . But when is the evidence strong enough to justify changing a practice ? Individual studies that involve only small numbers of patients may have results that are distorted by the r and om play of chance and thus lead to less than optimal decisions . As is clear from other papers in this series , systematic review s identify , critically appraise , and review all the relevant studies on a clinical question and are more likely to give a valid answer . They use explicit methods and quality st and ards to reduce bias . Their results are the closest we can come to reaching the truth given our current state of knowledge . The questions about an intervention that a systematic review should answer are the following : 1 . Does it work ? 2 . If it works , how well does it work in general and compared with placebo , no treatment , or other interventions that are currently in use ? 3 . Is it safe ? 4 . Will it be safe and effective for my patients ? Whereas the critical appraisal and qualitative synthesis provided by review articles can be interpreted directly , the numerical products of quantitative review s can be more difficult to underst and and apply in daily clinical practice . This paper provides guidance on how to interpret the numerical and statistical results of systematic review s , translate these results into more underst and able terms , and apply them directly to individual patients . Many of these principles can also be used to interpret the numerical results of individual clinical studies . They are particularly relevant to systematic review s , however , because such review s contain more information than do primary studies and often exert greater influence than do individual studies . Making Sense of the Numerical Results of Clinical Studies Although the results of clinical studies can be expressed in intuitively meaningful ways , such results do not always easily translate into clinical decision making . For example , results are frequently expressed in terms of risk , which is an expression of the frequency of a given outcome . ( Risks are probabilities , which can vary between 0.0 and 1.0 . A probability of 0.0 means that the event will never happen , and a probability of 1.0 means that it always happens . ) Consider a hypothetical study of the recurrence of migraine headaches in a control group receiving placebo and a treatment group receiving a new antimigraine preparation , drug M ( a secondary prevention trial ) . Suppose that at the end of the trial , migraines recurred in 30 % of the control group ( the risk for recurrence was 0.30 ) but in only 5 % of the drug M group ( risk of 0.05 ) ( Table 1 ) . Table 1 . Numerical Expression of Hypothetical Clinical Trial Results The outcomes of the study are clear enough for the two groups when they are examined separately . But clinicians and patients are more interested in the comparative results , that is , the outcome in one group relative to the outcome in the other group . This overall ( comparative ) result can be expressed in various ways . For example , the relative risk , which is the risk in the treatment group relative to that in the control group , is simply the ratio of the risks in the two groups . In other words , relative risk is the risk in the treatment group divided by that in the control group , 0.05 0.30 , or 0.17 . The comparison can also be expressed as the reduction in relative risk , which is the ratio between the decrease in risk ( in the treatment group ) and the risk in the control group , 0.25 0.30 , or 0.83 ( Table 1 ) . ( The relative risk reduction can also be calculated as 1 relative risk ) . Although the clinical meaning of relative risk ( and relative risk reduction ) is reasonably clear , relative risk has the distinct disadvantage that a given value ( for example , 0.17 ) is the same whether the risk with treatment decreases from 0.80 to 0.14 , from 0.30 to 0.05 , from 0.001 to 0.00017 , and so forth . The clinical implication s of these changes clearly differ from one another enormously and depend on the specific disease and intervention . An important alternate expression of comparative results , therefore , is the absolute risk reduction . Absolute risk reduction is determined by subtracting the risk in one group from the risk in the other ( for example , the risk in the treatment group is subtracted from the risk in the placebo group ) . In the case of our migraine study , the absolute risk reduction would be 0.30 0.05 , which equals 0.25 , or 25 percentage points . In contrast , for a study in which the risk decreased from 0.001 to 0.00017 , the absolute risk reduction would be only 0.00083 , or 0.083 percentage points , which is a trivial change in comparison ( Table 1 ) . This arithmetic emphasizes the difficulty of expressing the results of clinical studies in meaningful ways . Relative risk and relative risk reduction clearly give a quantitative sense of the effects of an intervention in proportional terms but provide no clue about the size of an effect on an absolute scale . In contrast , although it tells less about proportional effects , absolute risk says a great deal about whether an effect is likely to be clinical ly meaningful . Despite this benefit , even absolute risk is problematic because it is a dimensionless , abstract number ; that is , it lacks a direct connection with the clinical situation in which the patient and physician exist . However , another way of expressing clinical research results can provide that clinical link : the number needed to treat ( NNT ) . Number Needed To Treat The NNT for a given therapy is simply the reciprocal of the absolute risk reduction for that treatment [ 1 , 2 ] . In the case of our hypothetical migraine study ( in which risk decreased from 0.30 without treatment with drug M to 0.05 with treatment with drug M , for a relative risk of 0.17 , a relative risk reduction of 0.83 , and an absolute risk reduction of 0.25 ) , the NNT would be 1 0.25 , or 4 . In concrete clinical terms , an NNT of 4 means that you would need to treat four patients with drug M to prevent migraine from recurring in one patient . To emphasize the difference between the concepts embodied in NNT and relative risk , recall the various situations mentioned above , in all of which the relative risk was 0.17 but in which the absolute risk decreased from 0.80 to 0.14 in one case and from 0.001 to 0.00017 in another . Note that the corresponding NNTs in these two other cases are 1.5 and 1204 , respectively : that is , you would need to treat 1.5 and 1204 patients to obtain a therapeutic result in these two situations compared with 4 patients with drug M ( Table 1 ) . The NNT can be calculated easily and kept as a single numerical reminder of the effectiveness ( or , as we will see , the potential for harm ) of a particular therapy . As we suggested , the NNT has the crucial advantage of direct applicability to clinical practice because it shows the effort that is required to achieve a particular therapeutic target . The NNT has the additional advantage that it can be applied to any beneficial outcome or any adverse event ( when it becomes the number needed to harm [ NNH ] ) . The concept of NNT always refers to a comparison group ( in which patients receive placebo , no treatment , or some other treatment ) , a particular treatment outcome , and a defined period of treatment . In other words , the NNT is the number of patients that you will need to treat with drug or treatment A to achieve an improvement in outcome compared with drug or treatment B for a treatment period of C weeks ( or other unit of time ) . To be fully specified , NNT and NNH must always specify the comparator , the therapeutic outcome , and the duration of treatment that is necessary to achieve the outcome . Important Qualities of the Number Needed To Treat The NNT is treatment specific . It describes the difference between treatment and control in achieving a particular clinical outcome . Table 2 shows NNTs from a selection of systematic review s and large r and omized , controlled trials . Table 2 . Numbers Needed To Treat from Systematic Review s and R and omized , Controlled Trials A very small NNT ( that is , one that approaches 1 ) means that a 
    Output:
    