Design #2 is best because sources of systematic bias can be reduced as diffusion of the intervention is unlikely, and patients are carefully selected and monitored over time.

INCORRECT

The correct answer is (c).

Design #2 address several concerns inherent in Design #1. The only patients who will be studied will be those with breast cancer. Although this could raise questions about the generalizability of the results, it eliminates concerns about systematic bias caused by disease-related differences in treatment effect. Concerns about diffusion of the treatment are eliminated by the collection of comparison data from another site. The trade-off in this approach---data collection by different sets of nurses at the different institutions and the possibility that there may be institutional biases that affect the two groups differently---may be partially addressed by careful nurse training and a review of treatment practices at the two sites. A sample of 50 study patients and 50 comparator patients will be recruited for this study, another improvement over Design #1. Although the investigators may recognize that these sample sizes may not be large enough to show clinically meaningful differences related to the effect of the study intervention, there is no way to be certain and the number selected is a reasonable estimate given clinical experience. A power calculation based on accurate estimates is not possible given the lack of any information about the expected effects from the intervention, and without this, the needed sample size to show effects is a guess. The design ensures that there will be 50 patients per group with 4 months of follow-up data. There will be a larger number of patients overall (recruited patients who drop out before 4 months) and this allows flexibility in the analysis. In one analysis, an "intent-to-treat" type, all the patients who sign consent and receive the intervention will be included in the group comparisons; fatigue scores from the early drop-outs will be partially inferred by carrying forward the last recorded score. In a second analysis, only the 50 patients per group who provided complete 4 month follow-up data will be compared. Establishing a defined sample size for patients recruited and followed for a time is a significant improvement. The major remaining concern about Design #2 is the collection of follow-up data at varying times depending on the chemotherapy. Manipulation of the data could be done to yield a summary index, such as change in fatigue over time, but the approach could nonetheless result in a bias related to the ability of the assessment approach to capture changes in fatigue. For example, if fatigue typically peaks between two and four weeks after starting chemotherapy, patients undergoing assessment at two week intervals will be more likely to show change than those undergoing assessment at six week intervals. If the proportion of two week versus six week assessment patients is different at the two study sites, group differences could be wrongly attributed to the study intervention. Hopefully, the investigators are aware of these potential problems and run appropriate post-hoc statistical analyses to determine whether they have occurred. In sum, Design #2 could potentially yield credible data but could be better.