• Between-Subjects Designs
  • The IV is manipulated between separate (independent) groups of participants (statistically, these are also referred to as independent-samples designs, because the DV scores in the different levels of the IV are independent (i.e., uncorrelated), since they were obtained from different groups of participants
• Each participant is assigned to only one experimental condition/level of the IV
• Because of this, there is no chance of one treatment condition "contaminating" responses to another treatment condition.
• Contamination refers to carryover effects, or order effects:
• That is, if people were exposed to both levels of an IV, the effects of being in Condition 1 (e.g., a small dose of a drug) could "carry over" to Condition 2 (e.g., a large dose of the drug).
• In this example, there could be residual effects of the first exposure that could influence behavior in the second condition. Or the "order" in which a participant received the doses (e.g., small, then large vs. large, then small) could differentially affect scores on the DV.
• Clearly, carry-over effects cannot occur with a Between-S design, and you may have already figured out that a major strength of the Between-S design is avoiding carryover effects.
• However, a major disadvantage of the Between-S design is the potential nonequivalence between groups in the different conditions
  • Individual differences in response to experimental conditions is a fact of life in psychological research (indeed, Personality Psychology is the area that specifically addresses individual differences, and Testing/Measurement is the specialization concerned with assessment of individual differences--I strongly recommend taking both courses, especially if you are planning on applying to graduate school).
  • Recall our discussion of this issue in Chapter 6 regarding the probabilistic nature of scientific conclusions, and the "signal/noise" ratio in research. Individual differences contribute to the "noise" in psychological research. However, this is "factored into the equation" in statistical analyses (in fact, this is called the "error" term in inferential statistics), so we can live with this fact of life.
  • Where this becomes a problem is if these individual differences should get unevenly-distributed between conditions of the experiment such that they can exert a systematic influence on the differences in the DV.
    • This, of course, is our old arch enemy, confounding--the individual differences become confounded with the IV if the groups in the study differ significantly on this extraneous variable of individual differences
    • In our incentive-performance example in Chapter 6, if we inadvertantly assigned more high-ability P's to the $100 reward group than to the no-reward control group, we couldn't say whether better performance in the $100 was due to the incentive or due to the greater overall ability level in that group.
• Matching and randomization are two ways to attempt to control for individual differences as an extraneous variable.
  • Matching techniques are sometimes called "yoked" designs, because P's in the different conditions are assigned based on similar scores obtained on a pretest of some salient variable (that is, a theoretically-important variable, such as ability in the above example)
  • So we might administer a pretest on statistical ability to our pool of potential P's. We find two P's who achieved the same score on this pretest, then randomly assign one to the high-incentive group and the other to the no-incentive group.
  • Since all P's in the two groups have been matched (yoked), we can be confident that overall the two groups are equivalent on this extraneous variable (i.e., it becomes a "control variable," because it is held constant, thus eliminated as an alternative explanation of differences between the experimental conditions).
  • The problem is that we don't always know which individual difference variables need to be controlled through matching, and sometimes matching on one variable can create nonequivalence on another variable.
• Because of the above problem, randomization is typically the preferred method of controlling for individual differences.
  • By randomly assigning all P's to experimental conditions, we make it unlikely that any given individual difference variable varies systematically by uneven distribution between conditions.
  • Because chance determines assignment to conditions, it is not likely that there would be more high-ability P's in one condition than another (note that the individual differences are still there, they just are evenly distributed so that they don't exert a systematic, confounding influence--instead, they just get relegated to the "error" term in the statistical analysis).
• You have probably also figured out that while individual differences is a draw-back of the Between-S designs, a major advantage of Within-S designs is the avoidance of this problem by employing the same P's in all conditions
• Within-Subjects Designs
  • The IV is manipulated within one group of P's in this design (statistically referred to as correlated-samples designs, because the scores between the conditions are not independent--since they were obtained from the same P's, the scores will be correlated).
  • Each participant is assigned to all levels of the IV
    • Other terms used for this type of design are repeated-measures (because we repeat the measurement of the DV for each P in each experimental condition) and pre-post (before-after) designs, because sometimes the IV concerns the comparison of P's prior to the introduction of some variable (e.g., their "alertness" scores before taking a stimulant) to their scores on the same variable after receiving the experimental treatment (e.g., we remeasure alertness after participants have taken the stimulant).
    • Note that in the above types of designs, P's are serving as their "own controls," that is, they serve first as the "control group" (being tested before the drug) then serving again as the "experimental group" (being tested again after taking the drug).
  • Of course, all of the above discussion of the advantage of Between-S designs (avoiding carryover effects) is simultaneously the major disadvantage of Within-S designs: carryover effects are inherent in these designs.
    • Since all P's receive all levels of the IV, their reponses to one level of the IV could be "contaminated" by their exposure to the other levels of the IV.
    • In other words, the order of exposure to conditions can be confounded (there it is again!) with the effects of the IV
    • Recall that in the Stroop experiment (which we did using a within-S design), since everyone completed the tasks of the IV in the same order, this was confounded with the type of task (e.g., we don't know whether performance differences between the conditions were due to the task or due to an order effect, such as practice or fatigue).
  • Randomization is sometimes used to control for the confounding influence of order effects. Each participant completes the experimental conditions in a random order.
    • This is generally not the preferred method, since the relative ordinal position of a treatment (whether P's experience it first, second, or third...) may still vary between participants.
    • This is typically only used if there are a large number of treatment levels
  • Counterbalancing is the preferred method, because the order effects are evenly distributed across conditions.
    • Complete counterbalancing is easy in a simple two-condition experiment: Half of the P's receive Level 1 first, and the other half receive Level 2 first.
    • Thus, since each level occurs equally-frequently in the ordinal position of first or second, any carryover effects of going from Level 1 to Level 2 are "counterbalanced" (basically "cancelled out," though they're actually relegated to the statistical error term) by an equal number of P's who go from Level 2 to Level 1.
    • Complete counterbalancing is impractical when there are several levels of an IV, so researchers use one of two forms of "incomplete counterbalancing:"
      • A Latin square design is one where each treatment occurs equally often at each ordinal position in the experiment. The way to create these "magic squares" may seem confusing, but it's not hard to do (assuming an even number of levels of the IV)
        • Basically, if we had four conditions (A, B, C, D), we would write them down in that order for the first row of our square, and again in the first column:

  		Order
  Participant Number		1st position	2nd position	3rd position	4th position
  	P1	A	B	C	D
  	P2	B
  	P3	C
  	P4	D

• Then just fill in either the rows or columns in accending order:

		Order
Participant Number		1st position	2nd position	3rd position	4th position
	P1	A	B	C	D
	P2	B	C	D	A
	P3	C	D	A	B
	P4	D	A	B	C

• Note above that "A" occurs equally often in every ordinal position (it occurs once in the 1st, once in the 2nd, once in the 3rd, and once in the 4th position)

• A Balanced Latin square is "good-and-balanced," that is, each treatment precedes and follows each other treatment equally often.
  • The formula for creating the first row of this square is A, B, N, C, N-1, D, N-2, E, N-3,...where N = the number of treatments (again, this assumes an even number of conditions)
  • For example, if we had 6 conditions, the formula would be: A, B, F, C, E, D for the first row, then you can just complete the columns in ascending order:

  A	B	F	C	E	D
  B	C	A	D	F	E
  C	D	B	E	A	F
  D	E	C	F	B	A
  E	F	D	A	C	B
  F	A	E	B	D	C

  • If you examine the above table, you can see that "A" precedes "B" once and follows "B" once, "B" precedes "C" once and follows "C" once, etc.

CONTROL CONDITIONS

• So far in this course we have referred to the "control group" as the group which "does not receive the experimental condition." Remember that this is done to control for changes that occur in absence of the presumed causal variable (the treatment)--the control condition provides a no-treatment baseline to which the scores in the experimental group can be compared.
• Some experiments use a "control" group that does receive some sort of treatment, but a different level than the one of interest in the experimental condition, so we say that the control condition is "implicit" within the experiment.
• For example, rather can comparing $0 incentive to $100 incentive, we might compare $10 incentive to $100 incentive. Note, that while the "control group" of the latter (the $10 group) does receive some incentive, it is a relatively much smaller amount than the "experimental group" (the $100 group), so it is an implicit control in that it still provides a baseline for comparing the high-incentive group.
• Mixed Designs
  • In this chapter we have been so far describing designs that have only one IV. Recall from Chapter 6, that often more interesting experiments consist of two or more IV's (factorial designs--we will turn to an indepth look at these next in Chapter 8).
  • Sometimes researchers include one IV manipulated within-groups and a second IV manipulated between groups, these are called "mixed model designs," since they mix the two types of manipulations in the same experiment.
  • These designs are useful if the researcher is concerned about both avoiding carryover effects (so this IV would be manipulated as a between-S factor) and nonequivalence between groups (so this IV would be manipulated as a within-S factor)

CHOOSING AN EXPERIMENTAL DESIGN

• As you might have surmised by now, the answer to the question of which design to choose depends on which type of problem it is most important to avoid in the particular experiment: carryover effects or individual differences.
• This can be difficult to decide for the beginner, but some of the decision again involves common sense. However, there is no substitute for a good knowledge of the literature--that will provide the best guidance as to which problem is most important to avoid.
• You will get some practicing contrasting Between-S and Within-S designs in the homework for this chapter, and we will discuss the rationale for choosing one design over the other in different experimental contexts.