Parsons and colleagues  attribute differences between the conclusions of our systematic review  and theirs  to differences in the way the two reviews grouped studies for meta-analyses. We suggest different explanations for discordant conclusions about the effects of behavioral interventions on smoking cessation and weight gain.
First, the two reviews included somewhat different studies. Approximately 25–30% of the clinical trials analyzed in one review fail to overlap those included in the other review. Secondly, the two systematic reviews operationalized the weight gain outcome differently. Parsons et al.  analyzed weight gain only in those who abstained from smoking—a very small number of people—which led to comparing extremely small samples for the weight outcome (e.g. one group of three versus another group of seven). In contrast, when data were available, Spring and colleagues  analyzed weight gain among all those randomized (i.e. using intent-to-treat analysis per best clinical trials practice). Analyzing abstainers to eliminate a confounding effect of nicotine is appropriate when studying causal mechanisms for weight gain in a pharmacological experiment. When testing clinical practice policy, however, intent-to-treat analysis of all those randomized is necessary. Clinicians do not have the luxury of addressing weight gain among only those who stay abstinent. They are responsible for managing the smoking and weight status of all patients in the practice, many of whom will have gained weight because they quit smoking temporarily, even though they failed to maintain abstinence. For that reason, the correct denominator is the entire population of patients who were offered either treatment or control.
A third difference is that Spring and colleagues  used more conservative random-effects analysis whereas, for unclear reasons, Parsons et al.  used fixed effects. Parsons et al.'s  use of fixed effects was surprising given their emphasis on heterogeneity, especially as fixed-effects analysis ignores between-study variability and usually yields narrower confidence intervals and stronger P-values than random-effects analysis. Although many of Parsons et al.'s I2 tests were non-significant, heterogeneity was non-trivial for some subgroup comparisons, and the test for heterogeneity has low power that is exacerbated by the small sample sizes in most of their comparisons. Because generalization beyond the observed data set can be considered legitimate for random but not fixed-effects analysis, it is hazardous to extrapolate conclusions beyond the several studies in each of Parsons et al.'s  comparisons. The danger is amplified because their major grouping of interventions into generic versus individualized interventions appears to have been idiosyncratic and post hoc.
Parsons and colleagues  grouped together the two studies [4,5] for which abstinence was non-significantly but directionally less in a treatment that addressed smoking only, compared to a treatment that addressed both smoking and weight. They justified that grouping by suggesting that the two studies by Hall and colleagues  and Pirie and colleagues  were unique in giving participants only generic, non-individualized advice. Then, based upon that rationale, they extrapolated conclusions inappropriately from liberal fixed-effects analyses to draw the alarming conclusion that generic behavioral advice about smoking and weight management undermines abstinence. We disagree strongly with that interpretation and also believe that it mischaracterizes Hall et al.'s  and Pirie et al.'s  interventions. Rather than giving participants only generic, non-individualized advice, Pirie et al.  and Hall et al.  provided multiple sessions of group treatment that involved tailoring by both the group leader and participants. Additionally, Pirie and colleagues  individualized the prescribed rate of calorie reduction, physical activity increase and smoking reduction for participants, based upon their starting levels. Moreover, the strongest test of whether generic treatment has a worse effect on abstinence than individualized treatment comes from comparisons in which patients are randomized to either condition within a single trial. Two such comparisons exist among the studies included in the meta-analyses, and both fail to show an adverse effect. At 1-year follow-up, Hall and colleagues  found abstinence to be nearly identical in their individualized versus non-specific conditions (21% versus 22%). Similarly, Copeland et al.  found no difference in abstinence between their individualized versus non-individualized intervention.
Parsons et al.'s interpretation [1,3] that individualized intervention suppresses long-term weight gain also seems ill-founded. In addition to the analytical problems already mentioned (use of fixed-effects and abstainers-only analysis), findings were overstated. The authors argue that the weight-suppressing effect of individualized treatment was strengthened at 12 months compared to end of treatment . In fact, however, because confidence intervals widened, the weight-suppressing effect of treatment failed to reach the P < 0.05 level of significance at 12 months, even when using fixed-effects analysis.
A final irony bears noting. Parsons and colleagues [1,3] dismiss Spring et al.'s  suggestion that lengthening the duration of weight control intervention may offer a way to enhance long-term post-cessation weight control. However, in Parsons et al.'s own analyses , long-term weight suppression was maximized by the longest-duration weight control intervention. That intervention, carried out by Copeland and colleagues , lasted 38 weeks.
We suggest that it is time to stop discouraging weight-conscious smokers from quitting by reinforcing the unwarranted fear that trying to manage weight and smoking simultaneously produces harm.