Randy asked me to weigh in, and I will, but I'm in overload with several
summer projects and getting off to EAS Tuesday morning. I'll watch what
happens here, then add my two bits.
However, as a quick comment:
12 colonies per rep is my preference, but there's no universal rule, but
time and costs may force you to use fewer colonies - although I generally
argue against dropping down to anything less than 6 colonies per treatment.
If you are doing a trial where you've traditional comparative treatments,
having lots of colonies per treatment level is usually preferred. I can
say thought that you never want less than 3. 1 colony is an unreplicated
trial, two has a rep, but what if one has a low, the other a high value - do
you go with the average? With 3, you've at least got a tie breaker to show
a trend.
Now, for some studies, the goal may be to look at something different, such
as spatial distribution. In those cases, you may want lots of single
colonies, one per location, maximizing the number of locations. You can then
conduct something called a repeated measures trial. In essence, you
periodically sample all of the colonies, then compare them to themselves in terms
of how they've changed.
Regardless, you always need control colonies, and although stats tend to be
easier using a balanced data set (same number of colonies per rep), there
are cases where you may want more control colonies.
There are stats that can be used to decide the minimum number of colonies
per replicate - but you either need to have some data (so you know how
variable the measurement(s) are likely to be, or you have to opt for a higher
number of colonies just to be conservative - it is easy to under-estimate
variation.
Biggest mistakes both inexperienced and experienced researcher make: 1) no
control OR a control that really isn't a control, 2) inadequate
replication, and 3) pseudoreplication - a major problem in field studies where the
replicates often aren't truly replicates.
The other major area of methodological mistakes are two other common
statistical problems: 1) Different samples of bees from the same colony are
not a true replicate - you've got subfamilies in a colony, so all of the bees
share some common lineage. This is an very common mistake in pesticide
label registration trials - the entire study is based on samples of bees from
the same colony rather than samples of bees from different colonies. The
problem here is also that colonies vary in susceptibility - some are more,
some are less susceptible to the test chemical. You need to include the
range of susceptibility in your trials - since real world colonies vary in
susceptibility. You don't want to base the entire registration data on a
colony that is more or less resistant to the chemical.
2) for benchtop trials, 30 bees in a cup (cage) is not a replicate of 30,
it is a replicate of 1 (they all share the same environment, food, etc. If
you want replication, you need more cups with bees. 10 cups of 30 bees
is a replicate of 10, not 300. This is a BIG and obvious mistake, yet
several pesticide studies over past couple of years have made this one, and the
reviewers never noticed.
One relatively recent paper talks about replication in the hundreds of bees
and report df s (degrees of freedom) as something like 298. Then they
point to HIGHLY significant results. But in truth, their trial had df s of
as small as 1. Use the right df number and any supposed statistical
difference vanishes. This is a glaring mistake, but it made it through peer
review and got published.
jerry
***********************************************
The BEE-L mailing list is powered by L-Soft's renowned
LISTSERV(R) list management software. For more information, go to:
http://www.lsoft.com/LISTSERV-powered.html
Guidelines for posting to BEE-L can be found at:
http://honeybeeworld.com/bee-l/guidelines.htm
|
